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In Memory of Dr. Otto Loewi 
1873 - 1961 

Presented by 

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EDWARJ) jENNER 1749-182^^ 

^::grSS;i^tS5.*:^ -K^Sf^^ ^ ^«i**aff*:><s^ 

THOMAS HUXLEY 1 823- 1 895 

GREGOR MENDEL 1 822-1 884 






Professor of Animal Pathology, University of Cambridge 

" Scientific research is not itself a science; 
it is still an art or craft." — VV. H. George 




Library of Congress Catalog Card No. 57-14582 




Preface viii 

I. Preparation 

Study I 

Setting about the Problem 8 

II. Experimentation 

Biological experiments 13 

Planning and assessing experiments 19 

Misleading experiments 23 

III. Change 

Illustrations 27 

Role of chance in discoveries 31 

Recognising chance opportunities 34 

Exploiting opportunities 37 

IV. Hypothesis 

Illustrations 41 

Use of hypothesis in research 46 

Precautions in the use of hypothesis 48 

V. Imagination 

Productive thinking 53 

False trails 58 

Curiosity as an incentive to thinking 61 

Discussion as a stimulus to the mind 63 

Conditioned thinking 64 

VI. Intuition 

Definitions and illustrations 68 

Psychology of intuition 73 

Technique of seeking and capturing intuitions 76 

Scientific taste 78 

P/ yC'6 


VII. Reason 

Limitations and hazards 82 

Some safeguards in use of reason in research 86 

The role of reason in research 92 

VIII. Observation 

Illustrations 96 

Some general principles in observation 98 

Scientific observation 102 

IX. Difficulties 

Mental resistance to new ideas 106 

Opposition to discoveries 1 1 1 

Errors of interpretation 1 1 5 

X. Strategy 

Planning and organising research 121 

Different types of research 126 

The transfer method in research 129 

Tactics 131 

XI. Scientists 

Attributes required for research 1 39 

Incentives and rewards 142 

The ethics of research 1 45 

Different types of scientific minds 148 

The scientific fife 151 

Appendix i 60 

Bibliography 169 

Index 175 

(The reference numbers throughout the book refer to 
the numbers in the bibliography) 




I. Michael Faraday Frontispiece 

Edward Jenner 
Thomas Huxley 
Gregor Mendel 

Facing Page 

IL Claude Bernard 68 

Louis Pasteur 
Charles Darwin 
Paul Ehrligh 

in. Theobald Smith 69 

Walter B. Cannon 
Sir Frederick Gowland Hopkins 
Sir Henry Dale 

IV. Sir Alexander Fleming 100 

Sir Howard Florey 
G. S. Wilson 
Sir MagFarlane Burnet 

V. Max Plangk ioi 

Sir Ronald Fisher 
C. H. Andre WES 




ELABORATE apparatus plays an important part in the science 
of to-day, but I sometimes wonder if we are not inclined to 
forget that the most important instrument in research must always 
be the mind of man. It is true that much time and effort is devoted 
to training and equipping the scientist's mind, but little attention 
is paid to the technicalities of making the best use of it. There 
is no satisfactory book which systematises the knowledge available 
on the practice and mental skills — the art — of scientific investiga- 
tion. This lack has prompted me to write a book to serve as an 
introduction to research. My small contribution to the literature 
of a complex and difficult topic is meant in the first place for the 
student about to engage in research, but I hope that it may also 
interest a wider audience. Since my own experience of research 
has been acquired in the study of infectious diseases, I have 
written primarily for the student of that field. But nearly all the 
book is equally applicable to any other branch of experimental 
biology and much of it to any branch of science. 

I have endeavoured to analyse the methods by which dis- 
coveries have been made and to synthesise some generalisations 
from the views of successful scientists, and also to include certain 
other information that may be of use and interest to the young 
scientist. In order to work this material into a concise, easily 
understandable treatise, I have adopted in some places a frankly 
didaciic attitude and I may have over-simplified some of the 
issues. Nothing, however, could be further from my intentions 
than to be dogmatic. I have tried to deduce and state simply as 
many guiding principles of research as possible, so that the student 
may have some specific opinions laid before him. The reader is 
not urged to accept my views, but rather to look upon them as 
suggestions for his consideration. 

Research is one of those highly complex and subtle activities 
that usually remain quite unformulated in the minds of those who 
practise them. This is probably why most scientists think that it is 



not possible to give any formal instruction in how to do research. 
Admittedly, training in research must be largely self-training, 
preferably with the guidance of an experienced scientist in the 
handling of the actual investigation. Nevertheless, I believe that 
some lessons and general principles can be learnt from the experi- 
ence of others. As the old adage goes, " the wise man learns from 
the experience of others, the fool only from his own." Any train- 
ing, of course, involves much more than merely being "told how". 
Practice is required for one to learn to put the precepts into effect 
and to develop a habit of using them, but it is some help to be told 
what are the skills one should acquire. Too often I have been able 
to do Httle more than indicate the difficulties likely to be met — 
difficulties which we all have to face and overcome as best we can 
when the occasion arises. Yet merely to be forewarned is often a 

Scientific research, which is simply the search for new know- 
ledge, appeals especially to people who are individualists and their 
methods vary from one person to another. A policy followed by 
one scientist may not be suitable for another, and different 
methods are required in different branches of science. However, 
there are some basic principles and mental techniques that are 
commonly used in most types of investigation, at least in the 
biological sphere. Claude Bernard, the great French physiologist, 
said : 

" Good methods can teach us to develop and use to better 
purpose the faculties with which nature has endowed us, while 
poor methods may prevent us from turning them to good account. 
Thus the genius of inventiveness, so precious in the sciences, 
may be diminished or even smothered by a poor method, while 
a good method may increase and develop it. . . . In biological 
sciences, the role of method is even more important than in the 
other sciences because of the complexity of the phenomena and 
countless sources of error." ^^ 

The rare genius with a flair for research will not benefit from 
instruction in the methods of research, but most would-be research 
workers are not geniuses, and some guidance as to how to go about 
research should help them to become productive earher than they 
would if left to find these things out for themselves by the wasteful 
method of personal experience. A well-known scientist told me 



once that he purposely leaves his research students alone for some 
time to give them an opportunity to find their own feet. Such a 
policy may have its advantages in selecting those that are worth- 
while, on a sink or swim principle, but to-day there are better 
methods of teaching swimming than the primitive one of throw- 
ing the child into water. 

There is a widely held opinion that most people's powers of 
originahty begin to decline at an early age. The most creative 
years may have already passed by the time the scientist, if he 
is left to find out for himself, understands how best to conduct 
research, assuming that he will do so eventually. Therefore, if in 
fact it is possible by instruction in research methods to reduce his 
non-productive probationary period, not only will that amount 
of time in training be saved, but he may become a more pro- 
ductive worker than he would ever have become by the slower 
method. This is only a conjecture but its potential importance 
makes it worth considering. Another consideration is the risk that 
the increasing amount of formal education regarded as necessary 
for the intending research worker may curtail his most creative 
years. Possibly any such adverse effect could be offset by instruc- 
tion along the lines proposed. 

It is probably inevitable that any book which attempts to deal 
with such a wide and complex subject will have many defects. 
I hope the shortcomings of this book may provoke others whose 
achievements and experience are greater than mine to write about 
this subject and so build up a greater body of organised know- 
ledge than is available in the literature at present. Perhaps I have 
been rash in trying to deal with psychological aspects of research 
without having had any formal training in psychology; but I 
have been emboldened by the thought that a biologist venturing 
into psychology may be in no more danger of going seriously 
astray than would a psychologist or logician writing about bio- 
logical research. Most books on the scientific method treat it from 
the logical or philosophical aspect. This one is more concerned 
with the psychology and practice of research. 

I have had difficulty in arranging in a logical sequence the 
many diverse topics which are discussed. The order of the chapters 
on chance, hypothesis, imagination, intuition, reason and observa- 
tion is quite arbitrary. The procedure of an investigation is 


epitomised in the second section of Chapter One. Trouble has 
been taken to collect anecdotes showing how discoveries have 
been made, because they may prove useful to those studying the 
ways in which knowledge has been advanced. Each anecdote is 
cited in that part of the book where it is most apt in illustrating 
a particular aspect of research, but often its interest is not limited 
to the exemplification of any single point. Other anecdotes are 
given in the Appendix. I apologise in advance for referring in 
several places to my own experience as a source of intimate 

I sincerely thank many friends and colleagues to whom I am 
greatly indebted for helpful suggestions, criticism and references. 
The following kindly read through an early draft of the book and 
gave me the benefit of their impressions : Dr. M. Abercrombie, 
Dr. C. H. Andrewes, Sir Frederic Bartlett, Dr. G. K. Batchelor, 
Dr. A. C. Crombie, Dr. T. K. Ewer, Dr. G. S. Graham-Smith, 
Mr. G. C. Grindley, Mr. H. Lloyd Jones, Dr. G. Lapage, Sir 
Charles Martin, Dr. I. Macdonald, Dr. G. L. McClymont, Dr. 
Marjory Stephenson and Dr. D. H. Wilkinson. It must not be 
inferred, however, that these scientists endorse all the views 
expressed in the book. 


It is most gratifying to be able to add now that the methods of 
research outlined in this book have received endorsement by a 
considerable number of scientists, both in reviews and in private 
communications. I have not yet met any serious disagreement 
with the main principles. Therefore it is now possible to oflfer the 
book with greater confidence. 

I am deeply grateful to the many well-wishers who have written 
to me, some with interesting confirmation of views expressed in 
the book, and some drawing attention to minor errors. The 
alterations introduced in this second edition are for the most part 
minor revisions but the chapter on Reason has been partly 

Cambridge, July 1953. W.I.B.B. 




This edition differe only sUghdy from the previous one. The 
opportunity has been taken to make a few alterations, mostly of 
a minor nature, and add to the Appendix two good stories iUus- 
trating the role of chance. 

Cambridge, September 1957. W.I.B.B. 




" The lame in the path outstrip the swift 
who wander from it." — Francis Bacon 


THE research worker remains a student all his Ufe. Preparation 
for his work is never finished for he has to keep abreast with 
the growth of knowledge. This he does mainly by reading current 
scientific periodicals. Like reading the newspapers, this study 
becomes a habit and forms a regular part of the scientist's life. 

The 1952 edition of the World List of Scientific Periodicals 
indexes more than 50,000 periodicals. A simple calculation shows 
this is equivalent to probably two million articles a year, or 40,000 
a week, which reveals the utter impossibility of keeping abreast 
of more than the small fraction of the Uterature which is most 
pertinent to one's interest. Most research workers try to see 
regularly and at least glance through the titles of the articles in 
twenty to forty periodicals. As with the newspaper, they just skim 
through most of the material and read fully only those articles 
which may be of interest. 

The beginner would be well advised to ask an experienced 
research worker in his field which journals are the most important 
for him to read. Abstracting journals are of limited value, if only 
because they necessarily lag some considerable time behind the 
original journals. They do, however, enable the scientist to cover 
a wide range of Uterature and are most valuable to those who 
have not access to a large number of journals. Students need 
some guidance in ways of tracing references through indexing 
journals and catalogues and in using libraries. 

It is usual to study closely the Uterature deahng with the 
particular problem on which one is going to work. However, 
surprising as it may seem at first, some scientists consider that 
this is unwise. They contend that reading what others have 



written on the subject conditions the mind to see the problem in 
the same way and makes it more difficuh to find a new and fruit- 
ful approach. There are even some grounds for discouraging an 
excessive amount of reading in the general field of science in 
which one is going to work. Charles Kettering, who was associated 
with the discovery of tetraethyl lead as an anti-knock agent in 
motor fuels and the development of diesel engines usable in trucks 
and buses, said that from studying conventional text-books we 
fall into a rut and to escape from this takes as much effort as to 
solve the problem. Many successful investigators were not trained 
in the branch of science in which they made their most brilliant 
discoveries : Pasteur, Metchnikoff and Galvani are well-known 
examples. A sheepman named J. H. W. Mules, who had no 
scientific training, discovered a means of preventing blowfly 
attack in sheep in Australia when many scientists had failed. 
Bessemer, the discoverer of the method of producing cheap steel, 
said : 

" I had an immense advantage over many others dealing with 
the problem inasmuch as I had no fixed ideas derived from long 
established practice to control and bias my mind, and did not 
suffer from the general belief that whatever is, is right." 

But in his case, as with many such "outsiders", ignorance and 
freedom from established patterns of thought in one field were 
joined with knowledge and training in other fields. In the same 
vein is the remark by Bernard that " it is that which we do know 
which is the great hindrance to our learning not that which we do 
not know." The same dilemma faces all creative workers. Byron 
wrote : 

" To be perfectly original one should think much and read 
little, and this is impossible, for one must have read before one 
has learnt to think." 

Shaw's quip " reading rots the mind " is, characteristically, not 
quite so ridiculous as it appears at first. 

The explanation of this phenomenon seems to be as follows. 
When a mind loaded with a wealth of information contemplates 
a problem, the relevant information comes to the focal point of 



thinking, and if that information is sufficient for the particular 
problem, a solution may be obtained. But if that information is 
not sufficient — and this is usually so in research — then that mass 
of information makes it more difficult for the mind to conjure 
up original ideas, for reasons which will be discussed later. 
Further, some of that information may be actually false, in which 
case it presents an even more serious barrier to new and pro- 
ductive ideas. 

Thus in subjects in which knowledge is still growing, or where 
the particular problem is a new one, or a new version of one 
already solved, all the advantage is with the expert, but where 
knowledge is no longer growing and the field has been worked 
out, a revolutionary new approach is required and this is more 
Hkely to come from the outsider. The scepticism with which the 
experts nearly always greet these revolutionary ideas confirms 
that the available knowledge has been a handicap. 

The best way of meeting this dilemma is to read critically, 
striving to maintain independence of mind and avoid becoming 
conventionalised. Too much reading is a handicap mainly to 
people who have the wrong attitude of mind. Freshness of outlook 
and originality need not suffer greatly if reading is used as a 
stimulus to thinking and if the scientist is at the same time engaged 
in active research. In any case, most scientists consider that it is 
a more serious handicap to investigate a problem in ignorance 
of what is already known about it. 

One of the most common mistakes of the young scientist start- 
ing research is that he believes all he reads and does not distinguish 
between the results of the experiments reported and the author's 
interpretation of them. Francis Bacon said : 

" Read not to contradict and confute, nor to believe and take 
for granted . . . but to weigh and consider." ^ 

The man with the right outlook for research develops a habit 
of correlating what is read with his knowledge and experience, 
looking for significant analogies and generalisations. This method 
of study is one way in which hypotheses are developed, for 
instance it is how the idea of survival of the fittest in evolution 
came to Darwin and to Wallace. 

Successful scientists have often been people with wide interests. 



Their originality may have derived from their diverse knowledge. 
As we shall see in a later chapter on Imagination, originality 
often consists in linking up ideas whose connection was not pre- 
viously suspected. Furthermore, variety stimulates freshness of 
outlook whereas too constant study of a narrow field predisposes 
to dullness. Therefore reading ought not to be confined to the 
problem under investigation nor even to one's own field of science, 
nor, indeed, to science alone. However, outside one's immediate 
interests, in order to minimise time spent in reading, one can read 
for the most part superficially, relying on summaries and reviews 
to keep abreast of major developments. Unless the research 
worker cultivates wide interests his knowledge may get narrower 
and narrower and restricted to his own speciality. One of the 
advantages of teaching is that it obliges the scientist to keep 
abreast of developments in a wider field than he otherwise would. 

It is more important to have a clear understanding of general 
principles, without, however, thinking of them as fixed laws, than 
to load the mind with a mass of detailed technical infonnation 
which can readily be found in reference books or card indexes. 
For creative thinking it is more important to see the wood than 
the trees ; the student is in danger of being able to see only the 
trees. The scientist with a mature mind, who has reflected a good 
deal on scientific matters, has not only had time to accumulate 
technical details but has acquired enough perspective to see the 

Nothing that has been said above ought to be interpreted as 
depreciating the importance of acquiring a thorough grounding 
in the fundamental sciences. The value to be derived from super- 
ficial and "skim" reading over a wide field depends to a large 
extent on the reader having a background of knowledge which 
enables him quickly to assess the new work reported and grasp 
any significant findings. There is much truth in the saying that 
in science the mind of the adult can build only as high as the 
foundations constructed in youth will support. 

In reading that does not require close study it is a great help 
to develop the art of skim-reading. Skimming properly done 
enables one to cover a large amount of literature with economy 
of time, and to select those parts which are of special interest. 
Some styles of writing, of course, lend themselves more to skim- 



ming than others, and one should not try to skim closely reasoned 
or condensed writing or any work which one intends to make 
the object of a careful study. 

Most scientists find it useful to keep a card index with brief 
abstracts of articles of special interest for their work. Also the 
preparation of these abstracts helps to impress the salient features 
of an article in the memory. After reading quickly through the 
article to get a picture of the whole, one can go back to certain 
parts, whose full significance is then apparent, re-read these and 
make notes. 

The recent graduate during his first year often studies some 
further subject in order better to fit himself for research. In the 
past it has been common for English-speaking research students 
to study German if they had no knowledge of that language and 
had already learnt French at school. In the biological sciences I 
think students would now benefit more from taking a course in 
biometrics, the importance of which is discussed in the next 
chapter. In the past it was important to be able to read German, 
but the output of Germany in the biological and medical sciences 
has been very small during the last ten years, and it does not 
seem likely to be considerable for some years to come. Scientists 
in certain other countries, such as Scandinavia and Japan, who 
previously often published in the German language, are now 
publishing almost entirely in English, which, with the vast expan- 
sion of science in America as well as throughout the British 
Commonwealth is becoming the international scientific language. 
Unless the student of biology has a special reason for wanting to 
learn German, I think he could employ his time more usefully 
on other matters until German science is properly revived. In this 
connection it may be worth noting the somewhat unusual view 
expressed by the great German chemist, Wilhelm Ostwald, who 
held that the research student should refrain from learning 
languages. He considered that the conventional teaching of Latin, 
in particular, destroys the scientific outlook. ^'^ Herbert Spencer 
has also pointed out that the learning of languages tends to 
increase respect for authority and so discourage development of 
the faculty of independent judgment, which is so important, 
especially for scientists. Several famous scientists — including 
Darwin and Einstein — had a strong distaste for Latin, probably 



because their independent minds rebelled against developing the 
habit of accepting authority instead of seeking evidence. 

The views expressed in the preceding paragraph on the possible 
harmful effect of learning languages are by no means widely 
accepted. However, there is another consideration to be taken 
into account when deciding whether or not to study a language, 
or for that matter any other subject. It is that time and effort 
spent in studying subjects not of great value are lost from the 
study of some other subject, for the active-minded scientist is 
constantly faced with what might be called the problem of com- 
peting interests : he rarely has enough time to do all that he 
would like to and should do, and so he has to decide what he 
can afford to neglect. Bacon aptly said that we must determine 
the relative value of knowledges. Cajal decries the popular idea 
that all knowledge is useful; on the contrary, he says, learning 
unrewarding subjects occupies valuable time if not actual space 
in the mind.^^° However, I do not wish to imply that subjects 
should be judged on a purely utilitarian basis. It is regrettable 
that we scientists can find so little time for general Hterature. 

If the student cannot attend a course in biometrics, he can 
study one of the more easily understood books or articles on 
the subject. The most suitable that have come to my notice 
are those of G. W. Snedecor,*'^ which deals with the applica- 
tion of statistics to animal and plant experimentation, and 
A. Bradford HilV^ which deals mainly with statistics in human 
medicine. Topley and Wilson's text-book of bacteriology con- 
tains a good chapter on the application of biometrics to bacteri- 
ology.^^ Professor R. A. Fisher's two books are classical works, 
but some people find them too difficult for a beginning.^ ^' ^° 
It is not necessary for the biologist to become an expert at 
biometrics if he has no liking for the subject, but he ought 
to know enough about it to avoid either undue neglect or 
undue respect for it and to know when he should consult a 

Another matter to which the young scientist might well give 
attention is the technique and art of writing scientific papers. 
The general standard of English in scientific papers is not high 
and few of us are above criticism in this matter. The criticism 
is not so much against the inelegance of the English as lack of 



clarity and accuracy. The importance of correct use of language 
lies not only in being able to report research well; it is with 
language that we do most of our thinking. There are several 
good short books and articles on the writing of scientific papers. 
Trelease'^ deals particularly with the technicalities of writing 
and editing and Kapp" and Allbutt^ are mainly concerned with 
the writing of suitable English. Anderson' has written a useful 
paper on the preparation of illustrations and tables for scientific 
papers. I have found that useful experience can be gained by 
writing abstracts for publication. Thereby one becomes familiar 
with the worst faults that arise in reporting scientific work and at 
the same time one is subjected to a salutary discipline in writing 

The scientist will find his life enriched and his understanding 
of science deepened by reading the lives and works of some of 
the great men of science. Inspiration derived from this source 
has given many young scientists a vision that they have carried 
throughout their lives. Two excellent recent biographies I can 
recommend are Ehibos' Louis Pasteur: Freelance of Science^^^ 
and Marquardt's Paul Ehrlich.^^^ In recent years more and more 
attention is being given to the study of the history of science 
and every scientist ought to have at least some knowledge of this 
subject. It provides an excellent corrective to ever-increasing 
specialisation and broadens one's outlook and understanding of 
science. There are books which treat the subject not as a mere 
chronicle of events but with an insight which gives an apprecia- 
tion of the growth of knowledge as an evolutionary process 
(e.g. ^°" ^^). There is a vast literature dealing with the philosophy 
of science and the logic of scientific method. Whether one takes 
up this study depends upon one's personal inclinations, but, 
generally speaking, it will be of little help in doing research. 

It is valuable experience for the young scientist to attend 
scientific conferences. He can there see how contributions to 
knowledge are made by building on the work of others, how 
papers are criticised and on what basis, and learn something of 
the personalities of scientists working in the same field as him- 
self It adds considerablv to the interest of research to be 
personally acquainted with the authors of the papers one reads, 
or even merely to know what they look like. Conferences also 



provide a good demonstration of the healthy democracy of 
science and the absence of any authoritarianism, for the most 
senior members are as Uable to be criticised as is anyone else. 
Every opportunity should be taken to attend occasional special 
lectures given by eminent scientists as these can often be a rich 
source of inspiration. For instance, F. M. Burnet^^ said in 1944 
that he had attended a lecture in 1920 by Professor Orme 
Masson, a man with a real feeUng for science, who showed with 
superb clarity both the coming progress in atomic physics and 
the intrinsic deUght to be found in a new understanding of 
things. Burnet said that although he had forgotten most of the 
substance of that lecture, he would never forget the stimulus it 

Setting about the Problem 

In starting research obviously one has first to decide what prob- 
lem to investigate. While this is a matter on which consultation 
with an experienced research worker is necessary, if the research 
student is mainly responsible for choosing his own problem 
he is more likely to make a success of it. It will be something 
in which he is interested, he will feel that it is all his own and 
he will give more thought to it because the responsibility of 
making a success of it rests on himself It is wise for him to 
choose a subject within the field which is being cultivated by 
the senior scientists in his laboratory. He will then be able to 
benefit from their guidance and interest and his work will increase 
his understanding of what they are doing. Nevertheless, if a 
scientist is obliged to work on a given problem, as may be the 
case in applied research, very often an aspect of real interest 
can be found if he gives enough thought to it. It might even 
be said that most problems are what the worker makes them. 
The great American bacteriologist Theobald Smith said that 
he always took up the problem that lay before him, chiefly 
because of the easy access of material, without which research 
is crippled. ^^ The student with any real talent for research 
usually has no difficulty in finding a suitable problem. If he 
has not in the course of his studies noticed gaps in knowledge, 
or inconsistencies, or has not developed some ideas of his own, 



it does not augur well for his future as a research worker. It is 
best for the research student to start with a problem in which 
there is a good chance of his accomplishing something, and, 
of course, which is not beyond his technical capabilities. Success 
is a tremendous stimulus and aid to further progress whereas 
continued frustration may have the opposite effect. 

After a problem has been selected the next procedure is to 
ascertain what investigations have already been done on it. 
Text-books, or better, a recent review article, are often useful 
as starting points, since they give a balanced summary of 
present knowledge, and also provide the main references. A text- 
book, however, is only a compilation of certain facts and hypo- 
theses selected by the author as the most significant at the time of 
writing, and gaps and discrepancies may have been smoothed 
out in order to present a coherent picture. One must, there- 
fore, always consult original articles. In each article there are 
references to other appropriate articles, and trails followed up in 
this way lay open the whole literature on the subject. Indexing 
journals are useful in providing a comprehensive coverage of 
references on any subject to within a year or so of the present, 
and where they cease a search is necessary in appropriate 
individual journals. The Quarterly Cumulative Index Medicus, 
Zoological Record^ Index Veterinarius and the Bibliography of 
Agriculture are the standard indexing journals in their respec- 
tive spheres. Trained librarians know how to survey literature 
systematically and scientists fortunate enough to be able to call 
on their services can obtain a complete list of references on any 
particular subject. It is advisable to make a thorough study of 
all the relevant literature early in the investigation, for much 
effort may be wasted if even only one significant article is missed. 
Also during the course of the investigation, as well as watching 
for new articles on the problem, it is very useful to read super- 
ficially over a wide field keeping constant watch for some new 
principle or technique that may be made use of 

In research on infectious diseases usually the next step is to 
collect as much firsthand information as possible about the 
actual problem as it occurs locally. For instance, if an animal 
disease is being investigated, a common procedure is to carry 
out field observations and make personal enquiries from farmers. 



This is an important prerequisite to any experimental work, 
and occasionally investigators who have neglected it undertake 
laboratory work which has little relation to the real problem. 
Appropriate laboratory examination of specimens is usually 
carried out as an adjunct to this field work. 

Farmers, and probably lay people generally, not infrequently 
colour their evidence to fit their notions. People whose minds are 
not disciplined by training often tend to notice and remember 
events that support their views and forget others. Tactful and 
searching enquiry is necessary to ascertain exactly what they have 
observed — to separate their observations from their interpreta- 
tions. Such patient enquiry is often well repaid, for farmers have 
great opportunities of gathering information. The important 
discovery that ferrets are susceptible to canine distemper acose 
from an assertion of a gamekeeper. His statement was at first 
not taken seriously by the scientists, but fortunately they later 
decided to see if there was anything in it. It is said that for 
two thousand years the peasants of Italy have believed that 
mosquitoes were concerned with the spread of malaria although 
it was only about fifty years ago that this fact was established by 
scientific investigation. 

It is helpful at this stage to marshal and correlate all the data, 
and to try to define the problem. For example, in investigating 
a disease one should try to define it by deciding what are its 
manifestations and so distinguish it from other conditions with 
which it may be confused. Hughlings Jackson is reported to 
have said : " The study of the causes of things must be preceded 
by the study of things caused." To show how necessary this is, 
there is the classical example of Noguchi isolating a spirochaete 
from cases of leptospiral jaundice and reporting it as the cause of 
yellow fever. This understandable mistake delayed yellow fever 
investigations (but the rumour that it led to Noguchi's suicide 
has no basis in fact). Less serious instances are not infrequently 
seen closer at hand. 

The investigator is now in a position to break the problem 
down into several formulated questions and to start on the 
experimental attack. EKiring the preparatory stage his mind will 
not have been passively taking in data but looking for gaps 
in the present knowledge, differences between the reports of 



different writers, inconsistencies between some observed aspect 
of the local problem and previous reports, analogies with related 
problems, and for clues during his field observations. The active- 
minded investigator usually finds plenty of scope for the formula- 
tion of hypotheses to explain some of the information obtained. 
From the hypotheses, certain consequences can usually be proved 
or disproved by experiment, or by the collection of further 
observational data. After thoroughly digesting the problem in 
his mind, the investigator decides on an experiment which is 
likely to give the most useful information and which is within 
the limitations of his own technical capacity and the resources 
at his disposal. Often it is advisable to start on several aspects 
of the problem at the same time. However, efforts should not 
be dispersed on too wide a front and as soon as one finds some- 
thing significant it is best to concentrate on that aspect of the 

As with most undertakings, the success of an experiment 
depends largely on the care taken with preliminary preparations. 
The most effective experimenters are usually those who give 
much thought to the problem beforehand and resolve it into 
crucial questions and then give much thought to designing experi- 
ments to answer the questions. A crucial experiment is one which 
gives a result consistent with one hypothesis and inconsistent with 
another. Hans Zinsser writing of the great French bacteriologist, 
Charles Nicolle, said : 

" Nicolle was one of those men who achieve their successes by 
long preliminary thought before an experiment is formulated, 
rather than by the frantic and often ill-conceived experimental 
activities that keep lesser men in ant-like agitation. Indeed, I have 
often thought of ants in observing the quantity output of ' what- 
of-it ' literature from many laboratories. . . . Nicolle did relatively 
few and simple experiments. But every time he did one, it was 
the result of long hours of intellectual incubation during which 
all possible variants had been considered and were allowed for 
in the final tests. Then he went straight to the point, without 
wasted motion. That was the method of Pasteur, as it has been 
of all the really great men of our calling, whose simple, conclu- 
sive experiments are a joy to those able to appreciate them."^°® 

Sir Joseph Barcroft, the great Cambridge physiologist, is said to 
have had the knack of reducing a problem to its simplest elements 



and then finding an answer by the most direct means. The general 
subject of planning research is discussed later under the tide 
" Tactics ". 


One of the research worker's duties is to follow the scientific 
literature, but reading needs to be done with a critical, reflective 
attitude of mind if originaUty and freshness of outlook are not 
to be lost. Merely to accumulate information as a sort of capital 
investment is not sufficient. 

Scientists tend to work best on problems of their own choice 
but it is advisable for the beginner to start on a problem which 
is not too difficult and on which he can get expert guidance. 

The following is a common sequence in an investigation on 
a medical or biological problem, (a) The relevant literature is 
critically reviewed. (6) A thorough collection of field data or 
equivalent observational enquiry is conducted, and is supple- 
mented if necessary by laboratory examination of specimens. 

(c) The information obtained is marshalled and correlated and 
the problem is defined and broken down into specific questions. 

(d) Intelligent guesses are made to answer the questions, as many 
hypotheses as possible being considered, (e) Experiments are 
devised to test first the likeliest hypotheses bearing on the most 
crucial questions. 




" The experiment serves two purposes, often independent 
one from the other: it allows the observation of new facts, 
hitherto either unsuspected, or not yet well defined; and it 
determines whether a working hypothesis fits the world of 
observable facts." — Rene J. Dubos. 

Biological experiments 

SCIENCE as we know it to-day may be said to date from the 
introduction of the experimental method during the 
Renaissance. Nevertheless, important as experimentation is in 
most branches of science, it is not appropriate to all types of 
research. It is not used, for instance, in descriptive biology, 
observational ecology or in most forms of clinical research in 
medicine. However, investigations of this latter type make use 
of many of the same principles. The main difference is that 
hypotheses are tested by the collection of information from 
phenomena which occur naturally instead of those that are 
made to take place under experimental conditions. In writing 
the last part of the previous chapter and the first part of this 
one I have had in mind the experimentalist, but there may be 
some points of interest in these also for the purely observational 

An experiment usually consists in making an event occur under 
known conditions where as many extraneous influences as possible 
are eliminated and close observation is possible so that relation- 
ships between phenomena can be revealed. 

The " controlled experiment " is one of the most important 
concepts in biological experimentation. In this there are two 
or more similar groups (identical except for the inherent vari- 
ability of all biological material); one, the "control" group, is 
held as a standard for comparison, while the other, the " test " 
group, is subjected to some procedure whose effect one wishes to 



determine. The groups are usually formed by ' randomisation ', 
that is to say, by assigning individuals to one group or the other 
by drawing lots or by some other means that does not involve 
human discrimination. The traditional method of experimenta- 
tion is to have the groups as similar as possible in all respects 
except in the one variable factor under investigation, and to 
keep the experiment simple. " Vary one thing at a time and make 
a note of all you do." This principle is still widely followed, 
especially in animal experiments, but with the aid of modem 
statistical techniques it is now possible to plan experiments to test 
a number of variables at the same time. 

As early as possible in an investigation, a simple crucial experi- 
ment should be carried out in order to determine whether or not 
the main hypothesis under consideration is true. The details 
can be worked out later. Thus it is usually advisable to test the 
whole before the parts. For example, before you try to reproduce 
a disease with a pure culture of bacteria it is usually wise to 
attempt transmission with diseased tissue. Before testing chemical 
fractions for toxicity, antigenicity or some other effect, first test 
a crude extract. Simple and obvious as this principle appears, 
it is not infrequently overlooked and consequently time is wasted. 
Another application of the same principle is that in making 
a first test of the effect of some quantitative factor it is usually 
advisable to determine at the outset whether any effect is pro- 
duced under extreme conditions, for example, with a massive dose. 

Another general principle of a rather similar kind is the process 
of systematic elimination. This method is well exemplified in the 
guessing game where a series of questions such as " animal, 
vegetable or mineral " is asked. One can often find the unknown 
more quickly by systematically narrowing down the possibiUties 
than by making direct but blind guesses. This principle is used 
in weighing, when weights that are too heavy and too light 
are tried, and then the two extremes are gradually brought 
together. The method is especially useful in seeking an unknown 
substance by chemical means, but it also has many applications 
in various branches of biology. In investigating the cause of a 
disease, for instance, sometimes one eliminates the various 
alternatives until at last a narrow field is left for one to 
concentrate on. 


In biology it is often good policy to start with a modest 
preliminary experiment. Apart from considerations of economy, 
it is seldom desirable to undertake at the outset an elaborate 
experiment designed to give a complete answer on all points. It 
is often better for the investigation to progress from one point 
to the next in stages, as the later experiments may require 
modification according to the results of the earher ones. One 
type of preliminary experiment is the " pilot " experiment, 
which is often used when human beings or farm animals are the 
subjects. This is a small-scale experiment often carried out at 
the laboratory to get an indication as to whether a full-scale 
field experiment is warranted. Another type of preliminary 
experiment is the "sighting" experiment done to guide the 
planning of the main experiment. Take, for example, the case 
of an in vivo titration of an infective or toxic agent. In the 
sighting experiment dilutions are widely spaced (e.g. hundred- 
fold) and few animals (e.g. two) are used for each dilution. 
When the results of this are available, dilutions less widely 
spaced (e.g. fivefold) are chosen just staggering the probable 
end-point, and larger groups of animals (e.g. five) are used. In 
this way one can attain an accurate result with the minimum 
number of animals. 

The so-called " screening " test is also a type of preliminary 
experiment. This is a simple test carried out on a large number 
of substances with the idea of finding out which of them warrant 
further trial, for example, as therapeutic agents. 

Occasionally quite a small experiment, or test, can be arranged 
so as to get a provisional indication as to whether there is any- 
thing in an idea which alone is based on evidence too slender 
to justify a large experiment. A sketchy experiment of this nature 
sometimes can be so planned that the results will be of some 
significance if they turn out one way though of no significance 
if the other way. However, there is a minimum below which 
it is useless to reduce the " set up " of even a preliminary 
experiment. If the experiment is worth doing at all it must be 
planned in such a way that it has at least a good chance of 
giving a useful result. The young scientist is often tempted 
through impatience, and perhaps lack of resources, to rush in 
and perform ill-planned experiments that have httle chance of 



giving significant results. Sketchy experiments are only justifiable 
when preliminary to more elaborate experiments planned to 
give a reUable result. Each stage of the investigation must be 
established beyond reasonable doubt before passing on to the 
next, or else the work may be condemned, quite properly, as 
being "sloppy". 

The essence of any satisfactory experiment is that it should 
be reproducible. In biological experiments it not infrequently 
happens that this criterion is difficult to satisfy. If the results of 
the experiment vary even though the known factors have not 
been altered, it often means that some unrecognised factor or 
factors is affecting the results. Such occurrences should be 
welcomed, because a search for the unknown factor may lead 
to an interesting discovery. As a colleague remarked to me 
recently : " It is when experiments go wrong that we find things 
out." However, first one should see if a mistake has been made, 
as a technical error is the most common explanation. 

In the execution of the experiment it is well worth while 
taking the greatest care with the essential points of technique. 
By taking great pains and paying careful attention to the im- 
portant details the originator of a new technical method some- 
times is able to obtain results which other workers, who are less 
familiar with the subject or less painstaking, have difficulty in 
repeating. It is in this connection that Carlyle's remark that 
genius is an infinite capacity for taking pains is true. A good 
example is provided by Sir Almroth Wright's selection of the 
Rawlings strain of typhoid bacillus when he introduced vaccina- 
tion against that disease. Only quite recently, since certain 
techniques have become available, has it been found that the 
Rawlings strain was an exceptionally good strain for use in making 
vaccine. Wright had carefully chosen the strain for reasons which 
most people would have considered of no consequence. Theobald 
Smith, one of the few really great bacteriologists, said of 
research : 

" It is the care we bestow on apparently trifling, unattractive 

and very troublesome minutiae which determines the result." ^^ 

Some discrimination, however, should be used, for it is possible 
to waste time in elaborating unnecessary detail on unimportant 
aspects of the work. 



The careful recording of all details in experimental work is 
an elementary but important rule. It happens surprisingly often 
that one needs to refer back to some detail whose significance 
one did not realise when the experiment was carried out. The 
notes kept by Louis Pasteur afford a beautiful example of the 
careful recording of every detail. Apart from providing an 
invaluable record of what is done and what observed, note- 
taking is a useful technique for prompting careful observation. 

The experimenter needs to have a proper understanding of 
the technical methods he uses and to realise their limitations and 
the degree of accuracy attainable by each. It is essential to be 
thoroughly famihar with laboratory methods before using them 
in research and to be able to obtain consistent and reUable results. 
There are few methods that cannot at times go wrong and 
give misleading results and the experimenter should be able 
to detect trouble of this nature quickly. Where practicable, 
estimations and titrations of crucial importance should be checked 
by a second method. The scientist must also understand his 
apparatus. Modem complicated apparatus is often convenient 
but it is not always foolproof, and experienced scientists often 
tend to avoid it because they fear it may give misleading results. 

Difficulties often arise in organising experiments with subjects 
over which there is only limited control — human beings or 
valuable farm animals. Unless the basic needs of the controlled 
experiment can be satisfied it is better to abandon the attempt. 
Such a statement may appear self-evident, but not infrequently 
investigators find the difficulties too great and compromise on 
some arrangement that is useless. Large numbers in no way offset 
the necessity of a satisfactory control group. The outstanding 
illustration is supplied by the story of B.C.G. vaccination in 
children. This procedure was introduced twenty-five years ago 
and was then claimed to protect people against tuberculosis; but 
although a large number of experiments have since been carried 
out, there is still to-day controversy as to its value in preventing 
the disease in people of European stock. Most of the experiments 
have proved nothing because the controls were not strictly 
comparable. The review on B.C.G. vaccination by Professor 
G. S. Wilson provides a good lesson in the difficulties and pitfalls 
of experimentation. He concludes : 



" These results show how important it is when carrying out a 
controlled investigation on human subjects to do everything 
possible to ensure that the vaccinated and control children are 
similar in every respect, including such factors as age, race, sex, 
social, economic and housing conditions, intellectual level and 
co-operativeness of the parents, risk of exposure to infection, 
attendance at infant welfare or other clinics and treatment when 

in." 106 

Professor Wilson has pointed out to me in conversation that 
unless decisive experiments are done before an alleged remedy 
is released for use in human medicine, it is almost impossible 
subsequently to organise an experiment with untreated controls, 
and so the alleged remedy becomes adopted as a general practice 
without anyone knowing if it is really of any use at all. For 
example, Pasteur's rabies treatment has never been proved by 
proper experiment to prevent rabies when given to persons after 
they are bitten and some authorities doubt if it is of any value, 
but it is impossible now to conduct a trial in which this treatment 
is withheld from a control group of bitten persons. 

Sometimes it is a necessary part of a field experiment to keep 
the groups in different surroundings. In such experiments one 
cannot be sure that any differences observed are due to the 
particular factor under scrutiny and not to other variables 
associated with the different environments. This difficulty can 
sometimes be met by replicating both test and control groups 
so that any effects due to environment will be exposed and 
perhaps cancel out. If variables which are recognised but thought 
to be extraneous cannot be eliminated, it may be necessary to 
employ a series of control groups, or carry out a series of experi- 
ments, in order to isolate experimentally each known difference 
between the two populations being compared. 

Whenever possible the results of experiments should be assessed 
by some objective measurement. However, occasionally this 
cannot be done, as for instance where the results concern the 
severity of clinical symptoms or the comparison of histological 
changes. When there is a possibility of subjective influences 
affecting the assessment of results, it is important to attain 
objectivity by making sure that the person judging the results 
does not know to which group each individual belongs. No 



matter how objectively minded the scientist may believe him- 
self to be, it is very difficult to be sure that his judgment 
may not be subconsciously biased if he knows to which group 
the cases belong when he is judging them. The conscientious 
experimenter, being aware of the danger, may even err by 
biasing his judgment in the direction contrary to the expected 
result. Complete intellectual honesty is, of course, a first essential 
in experimental work. 

When the experiment is complete and the results have been 
assessed, if necessary with the aid of biometrics, they are 
interpreted by relating them to all that is already known about 
the subject. 

Planning and assessing experiments 

Biometrics, or biostatistics, the application of the methods of 
mathematical statistics to biology, is a comparatively new branch 
of science and its importance in research has only lately won 
general recognition. Books dealing with this subject have been 
mentioned in Chapter One and I do not intend to do more here 
than call attention to a few generalities and stress the need for 
the research worker to be acquainted at least with the general 
principles. Some knowledge of statistical methods is necessary 
for any form of experimental or observational research where 
numbers are involved, but especially for the more complex 
experiments where there is more than one variable. 

One of the first things which the beginner must grasp is that 
statistics need to be taken into account when the experiment is 
being planned, or else the results may not be worth treating 
statistically. Therefore biometrics is concerned not only with the 
interpretations of results but also with the planning of experi- 
ments. It is now usually taken as including, besides the purely 
statistical techniques, also the wider issues involved in their appli- 
cation to experimentation such as the general principles of the 
design of experiments and the logical issues concerned. Sir 
Ronald Fisher, who has done so much to develop biometrical 
methods, discusses these topics in his book, The Design of 

In selecting control and test groups, logic and common sense 
have first to be satisfied. A common fallacy, for instance, is to 
compare groups separated by time — the data of one year being 



compared to data obtained in previous years. Evidence obtained 
in this way is never conclusive, though it may be usefully sugges- 
tive. "If when the tide is falling you take out water with a 
twopenny pail, you and the moon can do a great deal." In 
biological investigations there may be many unsuspected factors 
that influence populations separated by time or geographically. 
When general considerations have been satisfied, statistical 
methods are used to decide on the necessary size of the groups, 
to select animals according to weight, age, etc. and, while taking 
these particulars into account, to distribute the animals into groups 
without sacrificing the principle of random selection. 

No two groups of animals or plants are ever exactly similar, 
owing to the inherent variabihty of biological material. Even 
though great pains are taken to ensure that all individuals in 
both groups are nearly the same in regard to sex, age, weight, 
breed, etc., there will always be variation that depends on factors 
not yet understood. It is essential to realise the impossibility of 
obtaining exactly similar groups. The difficulty must be met by 
estimating the variability and taking it into account when assess- 
ing the results. Within reasonable limits it is desirable to choose 
the animals for an experiment showing little variability one with 
another, but it is not essential to go to great lengths to achieve 
this. Its purpose is to increase the sensitivity of the experiment, 
but this can be done in other ways, such as by increasing the 
numbers in the groups. There are mathematical techniques for 
making corrections in certain cases for diflferences between 
individuals or groups. 

Another method of meeting the difficulty of variability in 
experimental animals is by " pairing " : the animals are arrayed 
in pairs closely resembling each other ( perhaps pairs of twins or 
litter mates). Each animal is compared only with its fellow and 
thus a series of experimental results is obtained. By using identical 
twins one can often effect great economy in numbers, which is 
important in investigations on animals that are expensive to buy 
and keep. Experiments carried out in New Zealand on butterfat 
yield showed that as much information was obtained per pair 
of identical twin cows as from two groups each of 55 cows. In 
experiments with growth rates, identical twins were about 25 
times more useful than ordinary calves.* 



When testing out a procedure for the first time it is often 
impossible to estimate in advance how many animals are required 
to ensure a decisive result. If expensive animals are involved 
economy may be effected by doing a test first with a few animals 
and repeating the test until the accumulated results are sufficient 
to satisfy statistical requirements. 

One of the basic conceptions in statistics is that the individuals 
in the group under scrutiny are a sample of an infinitely large, 
hypothetical population. Special techniques are available for 
random samphng and for estimating the necessary size of the 
sample for it to be representative of the whole. The number 
required in the sample depends on the variability of the material 
and on the degree of error that will be tolerated in the results, 
that is to say, on the order of accuracy required. 

Fisher considers that in the past there has been too much 
emphasis placed on the importance of varying only one factor 
at a time in experimentation and shows that there are distinct 
advantages in planning experiments to test a number of variables 
at the same time. Appropriate mathematical techniques enable 
several variables to be included in the one experiment, and this 
not only saves time and effort, but also gives more information 
than if each variable were treated separately. More information 
is obtained because each factor is examined in the light of a 
variety of circumstances, and any interaction between the factors 
may be detected. The traditional method of experimental isola- 
tion of a single factor often involves a somewhat arbitrary 
definition of that factor and the testing of it under restricted, 
unduly simphfied circumstances. Complex, multiple factor experi- 
ments, however, are not so often applicable to work with animals 
as to work with plants, although they can be used with advantage 
in feeding trials where various combinations of several com- 
ponents in the ration are to be tested. 

Statistics, of course, like any other research technique, has 
its uses and its limitations and it is necessary to understand its 
proper place and function in research. It is mainly valuable in 
testing an hypothesis, not in initiating a discovery. Discoveries 
may originate from taking into consideration the merest hints, 
the slightest diflferences in the figures between different groups, 
suggesting something to be followed up; whereas statistics are 



usually concerned with carefully pre-arranged experiments set up 
to test an idea already bom. Also, in trying to provide sufficient 
data for statistical analysis, the experimenter must not be tempted 
to do so at the expense of accurate observation and of care w^ith 
the details of the experiment. 

The use of statistics does not lessen the necessity for using 
common sense in interpreting results, a point which is sometimes 
forgotten. Fallacy is especially likely to arise in dealing with field 
data in which there may be a significant difference between two 
groups. This does not necessarily mean that the difference is 
caused by the factor which is under consideration because 
possibly there is some other variable whose influence or import- 
ance has not been recognised. This is no mere academic possi- 
bility, as is shown for example by the confusion that has arisen 
in many experiments with vaccination against tuberculosis, the 
common cold and bovine mastitis. Better hygienic measures 
and other circumstances which may influence the results are 
often coupled with vaccination. Statistics may show that people 
who smoke do not on the average five as long as people who do 
not smoke but that does not necessarily mean that smoking 
shortens life. It may be that people who do not smoke take more 
care of their health in other and more important ways. Such 
fallacies do not arise in well designed experiments where the 
initial process of randomisation ensures a valid comparison of 
the groups. 

The statistician, especially if he is not also a biologist, may be 
inclined to accept data given him for analysis as more reliable 
than they really are, or as being estimated to a higher degree of 
accuracy than was attempted. The experimenter should state 
that measurements have been made only to the nearest centi- 
metre, gram or whatever was the unit. It is helpful for the 
statistician to have had some personal experience of biological 
experimentation and he ought to be thoroughly familiar with all 
aspects of experiments on which he is advising. Close co-opera- 
tion between the statistician and the biologist can often enable 
enlightened common sense to by-pass a lot of abstruse mathe- 

Occasionally scientific reports are marred by the authors 
giving their results only as averages. Averages often convey 



little information and may even be misleading. The frequency 
distribution should be given and some figures relating to indiv- 
iduals are often helpful in giving a complete picture. Graphs also 
can be misleading and the data on which they are based needs 
to be examined critically. If the plotted points on a graph are 
not close together — that is, if the observations have not been 
made at frequent intervak — it is not always justifiable to connect 
them with straight or curved lines. Such lines may not represent 
the true position, for one does not know what actually occurred 
in the interval. There may, for instance, have been an unsuspected 
rise and fall. 

Misleading experiments 

Some of the hazards associated with the use of reason, hypo- 
thesis and observation in research are discussed in the appropriate 
chapters of this book. As a corrective to any tendency to put 
excessive faith in experimentation, it is as well here to remind 
the reader that experiments also can at times be quite misleading. 
The most common cause of error is a mistake in technique. 
Reliance cannot be placed on results unless the experimenter is 
thoroughly competent and familiar with the technical procedures 
he uses. Even in the expert's hands technical methods have to be 
constantly checked against known " positive " and " negative " 
specimens. Apart from technical slips, there are more subtle 
reasons why experiments sometimes " go wrong ". 

John Hunter deliberately infected himself with gonorrhoea to 
find out if it was a distinct disease from syphilis. Unfortunately 
the material he used to inoculate himself contained also the 
syphilis organism, with the result that he contracted both diseases 
and so established for a long time the false behef that both were 
manifestations of the same disease. Needham's experiments with 
flasks of broth led himself and others to believe that spontaneous 
generation was possible. Knowledge at the time was insufficient 
to show that the fallacy arose either from accidental contamina- 
tion or insufficient heating for complete sterilisation. In recent 
years we have seen an apparently weU-conducted experiment 
prove that patulin has therapeutic value against the common cold. 
Statistical requirements were well satisfied. But no one since has 



been able to show any benefit from patulin and why it seemed 
to be efficacious in the first experiment remains a mystery.^* 

When I saw a demonstration of what is known as the Mules 
operation for the prevention of blowfly attack in sheep, I realised 
its significance and my imagination was fired by the great 
potentialities of Mules' discovery. I put up an experiment involv- 
ing thousands of sheep and, without waiting for the results, 
persuaded colleagues working on the blowfly problem to carry 
out experiments elsewhere. When about a year later, the results 
became available, the sheep in my trial showed no benefit from 
the operation. The other trials, and all subsequent ones, showed 
that the operation conferred a very valuable degree of protec- 
tion and no satisfactory explanation could be found for the 
failure of my experiment. It was fortunate that I had enough 
confidence in my judgment to prevail upon my colleagues to put 
up trials in other parts of the country, for if I had been more 
cautious and awaited my results they would probably have 
retarded, the adoption of the operation for many years. 

Several large-scale experiments in the U.S.A. proved that 
immunisation greatly reduced the incidence of influenza in 1 943 
and again in 1945, yet in 1947 the same type of vaccine failed. 
Subsequently it was found that this failure was due to the 1947 
strain of virus being different from those current in earher years 
and used in making the vaccine. 

It is not at all rare for scientists in different parts of the world 
to obtain contradictory results with similar biological material. 
Sometimes these can be traced to unsuspected factors, for 
instance, a great difference in the reactions of guinea-pigs to diph- 
theria toxin was traced to a difference in the diets of the animals. 
In other instances it has not been possible to discover the 
cause of the disagreement despite a thorough investigation. In 
Dr. Monroe Eaton's laboratory in the United States influenza 
virus can be made to spread from one mouse to another, but in 
Dr. C. H. Andrewes' laboratory in England this cannot be 
brought about, even though the same strains of mice and virus, 
the same cages and an exactly similar technique are used. 

We must remember that, especially in biology, experimental 
results are, strictly speaking, only valid for the precise conditions 
under which the experiments were conducted. Some caution is 



necessary in drawing conclusions as to how widely applicable 
are results obtained under necessarily limited sets of circum- 

Darwin once said half seriously, " Nature will tell you a direct 
lie if she can." Bancroft points out that all scientists know from 
experience how difficult it often is to make an experiment come 
out correctly even when it is known how it ought to go. There- 
fore, he says, too much trust should not be put in an experiment 
done with the object of getting information.^" 

The examples quoted are experiments which gave results that 
were actually " wrong " or misleading. Fortunately they are 
exceptional. Commoner, however, is the failure of an experiment 
to demonstrate something because the exact conditions necessary 
are not known, such as Faraday's early repeated failures to obtain 
an electric current by means of a magnet. Such experiments 
demonstrate the well-known difficulty of proving a negative 
proposition, and the folly of drawing definite conclusions from 
them is usually appreciated by scientists. It is said that some 
research institutes deliberately destroy records of " negative 
experiments ", and it is a commendable custom usually not to 
publish investigations which merely fail to substantiate the hypo- 
thesis they were designed to test. 


The basis of most biological experimentation is the controlled 
experiment, in which groups, to which individuals are assigned at 
random, are comparable in all respects except the treatment under 
investigation, allowance being made for the inherent variability 
of biological material. Two useful principles are to test the whole 
before the part, and to ehminate various possibilities systemati- 
cally. In the execution of an experiment close attention to detail, 
careful note-taking and objectivity in the reading of results are 

Biometrics is concerned with the planning of experiments 
as well as the interpretation of results. A basic concept in 
biometrics is that there is an infinitely large, hypothetical popula- 
tion of which the experimental group or data are a random 
sample. The difficulty presented by the inherent variability of 



biological material is circumvented by estimating the variability 
and taking it into account when assessing the results. 

Experimentation, like other measures employed in research, is 
not infallible. Inability to demonstrate a supposition experi- 
mentally does not prove that it is incorrect. 




" Chance favours only those who know 
how to court her." — Charles Nicolle 


IT WILL be simpler to discuss the role of chance in research if 
we first consider some illustrative examples of discoveries in 
which it played a part. These anecdotes have been taken from 
sources believed to be authentic, and one reference is quoted 
for each although in many instances several sources have been 
consulted. Only ten are included in this section but seventeen 
others illustrating the role of chance are to be found in the 

Pasteur's researches on fowl cholera were interrupted by the 
vacation, and when he resumed he encountered an unexpected 
obstacle. Nearly all the cultures had become sterile. He attempted 
to revive them by sub-inoculation into broth and injection into 
fowls. Most of the sub-cultures failed to grow and the birds 
were not affected, so he was about to discard everything and 
start afresh when he had the inspiration of re-inoculating the 
same fowls with a fresh culture. His colleague Duclaux relates : 

" To the surprise of all, and perhaps even of Pasteur, who was 
not expecting such success, nearly all these fowls withstood the 
inoculadon, although fresh fowls succumbed after the usual 
incubation period." 

This resulted in the recognition of the principle of immunisation 
with attenuated pathogens.^ ^ 

The most important method used in staining bacteria is that 
discovered by the Danish physician G. Gram. He described how 
he discovered the method fortuitously when trying to develop a 
double stain for kidney sections. Hoping to stain the nuclei violet 
and the tubules brown, he used gentian violet followed by iodine 



solution. Gram found that after this treatment the tissue was 
rapidly decolourised by alcohol but that certain bacteria remained 
blue-black. The gentian violet and iodine had unexpectedly 
reacted with each other and with a substance present in some 
bacteria and not others, thus providing not only a good stain but 
also a simple test which has proved of the greatest value in 
distinguishing different bacteria. ^°^ 

While engaged in studying the function of the pancreas in 
digestion in 1889 at Strasbourg, Professors von Mering and 
Minkowski removed that organ from a dog by operation. Later 
a laboratory assistant noticed that swarms of flies were attracted 
by the urine of the operated dog. He brought this to the attention 
of Minkowski, who analysed the urine and found sugar in it. 
It was this finding that led to our understanding of diabetes and 
its subsequent control by insulin. ^^ More recently the Scotsman, 
Shaw Dunn, was investigating the cause of the kidney damage 
which follows a severe crush injury to a limb. Among other 
things he injected alloxan and he found that it caused necrosis 
of the islet tissue of the pancreas. This unexpected finding has 
provided a most useful tool in the study of diabetes.^^ 

The French physiologist, Charles Richet, was testing an extract 
of the tentacles of a sea anemone on laboratory animals to 
determine the toxic dose when he found that a small second dose 
given some time after the first was often promptly fatal. He 
was at first so astounded at this result that he could hardly believe 
that it was due to anything he had done. Indeed he said it was 
in spite of himself that he discovered induced sensitisation or 
anaphylaxis and that he would never have believed that it was 
possible." Another manifestation of the same phenomenon was 
discovered independently by Sir Henry Dale. He was applying 
serum to strips of involuntary muscle taken from guinea-pigs 
when he encountered one that reacted violently to the application 
of horse serum. Seeking an explanation of this extraordinary 
observation he found that that guinea-pig had some time 
previously been injected with horse serum. ^^ 

It was the usual practice among physiologists to use physio- 
logical saline as a perfusion fluid during experiments on isolated 
frogs' hearts. By this means they could be kept beating for 
perhaps half an hour. Once at the London University College 



Hospital a physiologist was surprised and puzzled to find his 
frogs' hearts continued to beat for many hours. The only possible 
explanation he could think of was that it was a seasonal effect 
and this he actually suggested in a report. Then it was found 
that the explanation was that his laboratory assistant had used 
tap water instead of distilled water to make up the saline solution. 
With this clue it was easy to determine what salts in the tap 
water were responsible for the increased physiological activity. 
This was what led Sidney Ringer to develop the solution which 
bears his name and which has contributed so much to experi- 
mental physiology. ^^ 

Dr. H. E. Durham has left the following written account of 
the discovery of agglutination of bacteria by antiserum. 

"It was a memorable morning in November 1894, when we 
had all made ready with culture and serum provided by Pfeiffer 
to test his diagnostic reaction in vivo. Professor Gruber called out 
to me ' Durham ! Kommen Sie her, schauen Sie an ! ' Before 
making our first injection with the mixtures of serum and vibrios, 
he had put a specimen under the microscope and there agglutina- 
tion was displayed. A few days later, we had been making our 
mixtures in small sterilised glass pots, it happened that none 
were ready sterilised, so I had to make use of sterile test-tubes; 
those containing the mixture of culture and serum were left 
standing for a short time and then I called, ' Herr Professor ! 
Kommen Sie her, schauen Sie an! ' the phenomenon of sedi- 
mentation was before his eyes! Thus there were two techniques 
available, the microscopic and the macroscopic." 

The discovery was quite unexpected and not anticipated by any 
hypothesis. It occurred incidentally in the course of another 
investigation, and macroscopic agglutination was found owing 
to the fortuitous lack of sterilised glass pots. [I am indebted to 
Professor H. R. Dean for showing me Durham's manuscript.] 
Gowland Hopkins, whom many consider the father of bio- 
chemistry, gave his practical class a certain well-known test for 
proteins to carry out as an exercise, but all the students failed to 
elicit the reaction. Investigation revealed that the reaction was 
only obtained when the acetic acid employed contained an 
impurity, glyoxylic acid, which thereafter became the standard 
test reagent. Hopkins followed up this clue further and sought 



the group in the protein with which the glyoxylic acid reacted, 
and this led him to his famous isolation of tryptophane.^* 

When Weil and Felix were investigating cases of louse-borne 
typhus in Poland in 19 15 they isolated the bacterium known as 
" Proteus X " from some patients. Thinking it might be the 
cause of the disease they tried agglutination of the organism 
with the patients' sera and obtained positive results. It was then 
found that Proteus X was not the causal organism of the disease ; 
nevertheless agglutination of this organism proved to be a reliable 
and most valuable means of diagnosing typhus. In the course 
of their experimental study of this serological reaction Weil and 
Felix identified the O and H antigens and antibodies, and this 
discovery in turn opened up a completely new chapter in serology. 
Later it was found that in Malaya those cases of typhus con- 
tracted in the scrub failed to show agglutination to Proteus X19. 
Strangely enough a new strain of Proteus, obtained from England 
and beUeved to be a typical strain of Proteus X19, agglutinated 
with sera from cases of scrub typhus but not with sera from the 
cases contracted in the town (shop typhus), which were reacting 
satisfactorily with the Proteus X19 strain that had been used in 
many parts of the world. Later it transpired that scrub typhus 
and shop typhus were two different rickettsial diseases. How it 
came about that the strain of Proteus sent out from England 
was not only not typical Proteus X19, but had changed to just 
what was wanted to diagnose the other disease, remains a 
profound mystery. ^^ 

Agglutination of red blood cells of the chick by influenza virus 
was first observed quite unexpectedly by Hirst and independently 
by McClelland and Hare when they were examining chick 
embryos infected with the virus. Fluid containing virus got mixed 
with blood cells which became agglutinated and the alert and 
observant scientists quickly followed up this clue. The discovery 
of this phenomenon has not only revolutionised much of our 
technique concerned with several viruses, but has opened up a 
method of approach to fundamental problems of virus-cell 
relationships.^^' ^" Following this discovery, other workers tried 
haemagglutination with other viruses and Newcastle disease, fowl 
plague and vaccinia were found to produce the phenomenon. 
However it was again by chance observation that haemagglutina- 



tion with the virus of mumps and later of mouse pneumonia 
was discovered. 

Rickettsiae (microbes closely related to viruses) cause typhus 
and several other important diseases and are difficult to cultivate. 
Dr. Herald Cox spent much time and effort trying to improve on 
methods of growing them in tissue culture and had tried adding 
all sorts of extracts, vitamins and hormones without achieving 
anything. One day while setting up his tests he ran short of chick 
embryo tissue for tissue culture, so to make up the balance he 
used yolk sac which previously he, like everyone else, had 
discarded. When he later examined these cultures, to his "amaze- 
ment and surprise", he found terrific numbers of the organisms 
in those tubes where he had happened to put yolk sac. A few 
nights later while in bed the idea occurred to him of inoculating 
the rickettsiae directly into the yolk sac of embryonated eggs. 
Getting out of bed at 4 a.m. he went to the laboratory and made 
the first inoculation of rickettsiae into the yolk sac. Thus was 
discovered an easy way of growing masses of rickettsiae, which 
has revolutionised the study of the many diseases they cause and 
made possible the production of effective vaccines against them. 
[Personal communication.] 

Role of chance in discovery 

These ten examples, together with nineteen others given in the 
Appendix and some of those in Chapters Four and Eight provide 
striking illustration of the important part that chance plays in 
discovery. They are the more remarkable when one thinks of the 
failures and frustrations usually met in research. Probably the 
majority of discoveries in biology and medicine have been come 
upon unexpectedly, or at least had an element of chance in them, 
especially the most important and revolutionary ones. It is scarcely 
possible to foresee a discovery that breaks really new ground, 
because it is often not in accord with current beliefs. Frequently 
I have heard a colleague, relating some new finding, say almost 
apologetically, " I came across it by accident." Although it is 
common knowledge that sometimes chance is a factor in the 
making of a discovery, the magnitude of its importance is seldom 
realised and the significance of its role does not seem to have 
been fully appreciated or understood. Books have been written on 



scientific method omitting any reference to chance or empiricism 
in discovery. 

Perhaps the most striking examples of empirical discoveries are 
to be found in chemotherapy where nearly all the great discoveries 
have been made by following a false hypothesis or a so-called 
chance observation. Elsewhere in this book are described the 
circumstances in which were discovered the therapeutic effects of 
quinine, salvarsan, sulphanilamide, diamidine, paraminobenzoic 
acid and penicillin. Subsequent rational research in each case 
provided only relatively small improvements. These facts are the 
more amazing when one thinks of the colossal amount of rational 
research that has been carried out in chemotherapy. 

The research worker should take advantage of this knowledge 
of the importance of chance in discovery and not pass over it 
as an oddity or, worse, as something detracting from the credit 
due to the discoverer and therefore not to be dwelt upon. 
Although we cannot deliberately evoke that will-o'-the-wisp, 
chance, we can be on the alert for it, prepare ourselves to 
recognise it and profit by it when it comes. Merely realising the 
importance of chance may be of some help to the beginner. We 
need to train our powers of observation, to cultivate that attitude 
of mind of being constantly on the look-out for the unexpected 
and make a habit of examining every clue that chance presents. 
Discoveries are made by giving attention to the slightest clue. 
That aspect of the scientist's mind which demands convincing 
evidence should be reserved for the proof stage of the investiga- 
tion. In research, an attitude of mind is required for discovery 
which is different from that required for proof, for discovery and 
proof are distinct processes. We should not be so obsessed with 
our hypothesis that we miss or neglect anything not directly 
bearing on it. With this in mind, Bernard insisted that, although 
hypotheses are essential in the planning of an experiment, once 
the experiment is commenced the observer should forget his 
hypothesis. People who are too fond of their hypotheses, he said, 
are not well fitted for making discoveries. The anecdote (related 
in Chapter Eight) about Bernard's work starting from the 
observation that the rabbits passed clear urine, provides a beauti- 
ful example of discovery involving chance, observation and a 
prepared mind. 



A good maxim for the research man is " look out for the 

It is unwise to speak of luck in research as it may confuse our 
thinking. There can be no objection to the word when it is used 
to mean merely chance, but for many people luck is a meta- 
physical notion which in some mystical way influences events, and 
no such concept should be allowed to enter into scientific thinking. 
Nor is chance the only factor involved in these unexpected 
discoveries, as we shall discuss more fully in the next section. 
In the anecdotes cited, many of the opportunities might well 
have been passed over had not the workers been on the look-out 
for anything that might arise. The successful scientist gives 
attention to every unexpected happening or observation that 
chance offers and investigates those that seem to him promising. 
Sir Henry Dale has aptly spoken of opportunism in this con- 
nection. Scientists without the flair for discovery seldom notice or 
bother with the unexpected and so the occasional opportunity 
passes without them ever being aware of it. Alan Gregg 
wrote : 

" One wonders whether the rare ability to be completely atten- 
tive to, and to profit by, Nature's slightest deviation from the 
conduct expected of her is not the secret of the best research 
minds and one that explains why some men turn to most remark- 
ably good advantage seemingly trivial accidents. Behind such 
attention lies an unremitting sensitivity."'*^ 

Writing of Charles Darwin, his son said : 

" Everybody notices as a fact an exception when it is striking 
and frequent, but he had a special instinct for arresting an 
exception. A point apparently slight and unconnected with his 
present work is passed over by many a man almost unconsciously 
with some half considered explanation, which is in fact no explan- 
ation. It was just these things that he seized on to make a start 
from." 28 

It is of the utmost importance that the role of chance be 
clearly understood. The history of discovery shows that chance 
plays an important part, but on the other hand it plays only 
one part even in those discoveries attributed to it. For this 
reason it is a misleading half-truth to refer to unexpected dis- 
coveries as " chance discoveries " or " accidental discoveries ". 



If these discoveries were made by chance or accident alone, 
as many discoveries of this type would be made by any 
inexperienced scientist starting to dabble in research as by 
Bernard or Pasteur. The truth of the matter lies in Pasteur's 
famous saying : "In the field of observation, chance favours 
only the prepared mind." It is the interpretation of the chance 
observation which counts. The role of chance is merely to 
provide the opportunity and the scientist has to recognise it and 
grasp it. 

Recognising chance opportunities 

In reading of scientific discoveries one is sometimes struck 
by the simple and apparently easy observations which have given 
rise to great and far-reaching discoveries making scientists 
famous. But in retrospect we see the discovery with its significance 
established. Originally the discovery usually has no intrinsic 
significance; the discoverer gives it significance by relating it 
to other knowledge, and perhaps by using it to derive further 
knowledge. The difficulties in the way of making discoveries 
in which chance is involved may be discussed under the following 

(a) Infrequency of opportunities. Opportunities, in the form 
of significant clues, do not come very often. This is the only 
aspect aflfected by sheer chance, and even here the scientist does 
not play a purely passive role. The successful researchers are 
scientists who spend long hours working at the bench, and who 
do not confine their activities to the conventional but try out 
novel procedures, therefore they are exposed to the maximum 
extent to the risk of encountering a fortunate " accident ". 

(b) Noticing the clue. Acute powers of observation are often 
required to notice the clue, and especially the ability to remain 
alert and sensitive for the unexpected while watching for the 
expected. Noticing is discussed at length in the chapter on 
observation, and it need only be said here that it is mainly a 
mental process. 

(c) Interpreting the clue. To interpret the clue and grasp its 
possible significance is the most difficult phase of all and requires 
the " prepared mind ". Let us consider some instances of 
failure to grasp opportunities. The history of discovery teems 



with instances of lost opportunities — clues noticed but their 
significance not appreciated. Before Rontgen discovered X-rays, 
at least one other physicist had noticed evidence of the rays 
but was merely annoyed. Several people now recall having 
noticed the inhibition of staphylococcal colonies by moulds 
before Fleming followed it up to discover penicillin. Scott, for 
instance, reports that he saw it and considered it only a nuisance 
and he protests against the view that Fleming's discovery was 
due to chance, for, he says, it was due mainly to his perspicacity 
in seizing on the opportunity others had let pass.*^ Another 
interesting case is related by J. T. Edwards. ^^ In 19 19 he noticed 
that one of a group of cultures of Brucella abortus grew much 
more luxuriantly than the others and that it was contaminated 
with a mould. He called the attention of Sir John M'Fadyean 
to this, suggesting it might be of significance, but was greeted 
with scorn. It was not till later that it was discovered that 
Br. abortus grew much better in the presence of CO2, which 
explains why Edwards' culture had grown much better in the 
presence of the mould. Bordet and others had casually noticed 
agglutination of bacteria by antisera, but none had seen the 
possibilities in it until Gruber and Durham did. Similarly, 
others had seen the phenomenon of bacteriophage lysis before 
Twort and D'Herelle. F. M. Burnet for one now admits having 
seen agglutination of chick embryos' red blood cells in the 
presence of influenza virus and probably others had too but 
none followed it up till G. K. Hirst, and McClelland and Hare. 
Many bacteriologists had seen rough to smooth colony variation 
in bacteria before Arkwright investigated it and found it to be 
associated with change in virulence and antigenicity. It is now, 
of course, one of the fundamental facts in immunology and 

Sometimes the significance of the clue which chance brings 
our way is quite obvious, but at others it is just a trivial incident 
of significance only for the well prepared mind, the mind loaded 
with relevant data and ripe for discovery. When the mind has 
a lot of relevant but loosely connected data and vague ideas, a 
clarifying idea connecting them up may be helped to crystallise 
by some small incident. Just as a substance may crystallise out 
of solution in the presence of a nucleus consisting of a minute 



crystal with the correct configuration, so did the falling apple 
provide a model for Newton's mind. Sir Henry Souttar has 
pointed out that it is the content of the observer's brain, 
accumulated by years of work, that makes possible the moment 
of triumph. This aspect of chance observation will be discussed 
further in the chapters on observation and on intuition. 

Anyone with an alertness of mind will encounter during the 
course of an investigation numerous interesting side issues that 
might be pursued. It is a physical impossibility to follow up all 
of these. The majority are not worth following, a few will reward 
investigation and the occasional one provides the opportunity of 
a lifetime. How to distinguish the promising clues is the very 
essence of the art of research. The scientist who has an indepen- 
dent mind and is able to judge the evidence on its merits rather 
than in light of prevailing conceptions is the one most likely to 
be able to realise the potentialities in something really new. He 
also needs imagination and a good fund of knowledge, to know 
whether or not his observation is new and to enable him to see 
the possible implications. In deciding whether a Hne of work 
should be followed, one should not be put off it merely because 
the idea has already been thought of by others or even been tried 
without it leading anywhere. This does not necessarily indicate 
that it is not good; many of the classic discoveries were 
anticipated in this way but were not properly developed until 
the right man came along. Edward Jenner was not the first to 
inoculate people with cowpox to protect them against smallpox, 
William Harvey was not the first to postulate circulation of the 
blood, Darwin was by no means the first to suggest evolution, 
Columbus was not the first European to go to America, Pasteur 
was not the first to propound the germ theory of disease, 
Lister was not the first to use carbolic acid as a wound antiseptic. 
But these men were the ones who fully developed these ideas 
and forced them on a reluctant world, and most credit rightly 
goes to them for bringing the discoveries to fruition. It is not 
only new ideas that lead to discoveries. Indeed few ideas are 
entirely original. Usually on close study of the origin of an 
idea, one finds that others had suggested it or something very 
like it previously. Charles NicoUe calls these early ideas that are 
not at first followed up, " precursor ideas ". 



Exploiting opportunities 
When a discovery has passed these hurdles and reached a 
stage where it is recognised and appreciated by its originator, 
there are still at least three more ways in which its general 
acceptance may be delayed. 

(d) Failure to follow up the initial finding. The initial disclosure 
may not be made the most of because it may not be followed up 
and exploited. The most productive scientists have not been 
satisfied with clearing up the immediate question but having 
obtained some new knowledge, they made use of it to uncover 
something further and often of even greater importance. 
Steinhaeuser discovered in 1840 that cod-liver oil cured rickets 
but this enormously important fact remained unproved and no 
more than an opinion for the next eighty years.^* In 1903 
Theobald Smith discovered that some motile baciUi may exist 
in culture as the normal motile form or as a non-motile variant, 
and he demonstrated the significance of these two forms in 
immunological reactions. This work passed almost unnoticed 
and was forgotten until the phenomenon was rediscovered in 
1 91 7 by Weil and FeUx. It is now regarded as one of the 
fundamental facts in immunological reactions.'^ Fleming 
described crude preparations of penicillin in 1929, but after a 
few years he dropped work on it without developing a therapeutic 
agent. He got no encouragement or assistance from others 
because they knew of many similar stories that had come to 
nothing. It was some years later that Florey took the work up 
from where Fleming left off and developed penicillin as a 
therapeutic agent. 

(e) Lack of an application. There may be no possible applica- 
tions of the discovery until years later. Neufeld discovered 
a rapid method of typing pneumococci in 1902, but it was not 
till 1 93 1 that it became of any importance when type-specific 
serum therapy was introduced. Landsteiner discovered the human 
blood groups in 1901, but it was not till anticoagulants were 
found and blood transfusion was developed in the 1 914—18 war 
that Landsteiner's discovery assumed importance and attracted 

(f ) Indifference and opposition. Finally the discovery has to 
run the gauntlet of scepticism and often resistance on the part 



of Others. This can be one of the most difficult hurdles of all 
and it is here that the scientist occasionally has to fight and in the 
past has sometimes even lost his life. The psychology of mental 
resistance to new ideas, and actual opposition to discoveries are 
discussed in a later chapter. 

Several of the points discussed in this and the preceding 
section may be illustrated by narrowing the story of Jenner's 
recognition of the potentialities of vaccination and his exploita- 
tion of it. Artificial immunisation against smallpox by means 
of inoculation with virulent smallpox material (variolation) had 
long been practised in the Orient. Some say that looo years B.C. 
it was the custom of China to insert material from smallpox 
lesions into the noses of children, others that variolation was 
introduced into China from India about a.d. iooo.^^' ^^' ^°* 
Variolation was introduced from Constantinople into England 
about the middle of the eighteenth century and became an 
accepted though not very popular practice about the time that 
Edward Jenner was bom. When Jenner was serving his appren- 
ticeship between thirteen and eighteen years of age, his attention 
was called to the local behef in Gloucestershire that people 
who contracted cow-pox from cattle were subsequently immune 
to smallpox. Jenner found that the local physicians were mostly 
familiar with the traditional belief but did not take it seriously, 
although they also were encountering instances of failure of 
people to develop infection when given variolation after they 
had had cow-pox. Jenner evidently kept the matter in mind 
for years without doing anything about it. After returning to 
country practice he confided in a friend that he intended trying 
vaccination. He divulged his intentions under a bond of secrecy 
because he feared ridicule if they should fail. Meanwhile he 
was exercising his genius for taking pains and making accurate 
observation by carrying out experiments in other directions. He 
was making observations on the temperature and digestion of 
hibernating animals for John Hunter, experimenting with agri- 
cultural fertilisers for Joseph Banks and on his own behalf 
carrying out studies on how the young cuckoo gets rid of its 
fellow nestlings. He married at thirty-eight and when his wife 
had a child he inoculated him with swine-pox and showed he 
was subsequently immune to smallpox. Still none of his colleagues 



— John Hunter among them — took much interest in Jenner's 
ideas about using cow-pox to vaccinate against smallpox and 
his first tentative paper on the subject was returned to him 
and apparently rejected. It was not till he was forty-seven years 
old (in the memorable year 1796) that he made his first 
successful vaccination from one human being to another. He 
transferred material from a pustule on the hand of a milkmaid, 
Sarah Nelmes, to an eight-year-old boy named James Phipps 
who thereby gained fame in the same odd way as did Joseph 
Meister for being the first person to receive Pasteur's treatment 
for rabies nearly a century later.* This is taken as the classical 
origin of vaccination but, as is often the case in the history of 
scientific discovery, the issue is not clear-cut. At least two others 
had actually performed it earUer but failed to follow it up. 
Jenner continued his experiments, and in 1798 published his 
famous Inquiry, reporting some twenty- three cases who were 
either vaccinated or had contracted cow-pox naturally and were 
subsequently shown to be immune to smallpox. Soon afterwards 
vaccination was taken up widely and spread throughout the 
world, despite severe opposition from certain quarters which 
curiously and interestingly enough persists even to-day in a fairly 
harmless form. Jenner suffered abuse but honours were soon 
showered on him from all quarters of the globe. ^^' ^^ 

This history provides an admirable demonstration of how 
difficult it usually is to recognise the true significance of a new 
fact. Without knowing the full history one might well suppose 
Jenner's contribution to medical science a very simple one not 
meriting the fame subsequently bestowed on it. But neither John 
Hunter nor any of Jenner's colleagues and contemporaries were 
able to grasp the potentialities in advance, and similar oppor- 
tunities had occurred and been let pass in other countries. There 
was an interval of thirty years after the experimentally minded 
Jenner himself became interested in the popular belief, before 
he performed the classical, crucial experiments. With our present 
conceptions of immunisation and of experimentation this may 
appear surprising but we must remember how revolutionary the 
idea was, even given the fact that variolation was an accepted 

* Meister remained at the Pasteur Institute as concierge until the occupa- 
tion of Paris by the Germans in 1940, when he committed suicide. 



practice. The fact that others who had the same opportunity 
failed to discover vaccination and that it took Jenner thirty 
years shows what a difficult discovery it was to make. Animals 
were at that time regarded with repugnance by most people 
so the idea of infecting a human being with a disease of animals 
created utmost disgust. All sorts of dire results were prophesied, 
including " cow-mania " and " ox-faced children " (one was 
actually exhibited ! ) . Like many great discoveries it did not 
require great erudition- and it mainly devolved on having bold- 
ness and independence of mind to accept a revolutionary idea 
and imagination to realise its potentialities. But Jenner also 
had practical difficulties to overcome. He found that cows 
were subject to various sores on the teats, some of which 
also affected the milkers but did not give immunity to small- 
pox. Even present day virus specialists have great difficulty 
in distinguishing between the different types of sores that 
occur on cows' teats; and the position is comphcated by 
observations suggesting that an attack of cow-pox does not confer 
immunity against a second attack of the same disease in the cow, 
a point Jenner himself noted. 

Jenner's discovery has its element of irony which so often lends 
additional interest to scientific anecdotes. Modem investigators 
believe that the strains of vaccinia now used throughout 
the world for many years are not cow-pox but have derived 
from smallpox. Their origin is obscure but it seems that in the 
early days cow-pox and smallpox got mixed up and an attenuated 
strain of smallpox developed and was mistakenly used for 


New knowledge very often has its origin in some quite un- 
expected observation or chance occurrence arising during an 
investigation. The importance of this factor in discovery should 
be fully appreciated and research workers ought deliberately to 
exploit it. Opportunities come more frequently to active bench 
workers and people who dabble in novel procedures. Interpreting 
the clue and realising its possible significance requires knowledge 
without fixed ideas, imagination, scientific taste, and a habit of 
contemplating all unexplained observations. 




" In science the primary duty of ideas is to be useful and 
interesting even more than to be ' true '." — Wilfred Trotter 


THE role of hypothesis in research can be discussed more 
effectively if we consider first some examples of discoveries 
which originated from hypotheses. One of the best illustrations 
of such a discovery is provided by the story of Christopher 
Columbus' voyage ; it has many of the features of a classic dis- 
covery in science, {a) He was obsessed with an idea — that since 
the world is round he could reach the Orient by sailing west, 
(b) the idea was by no means original, but evidently he had 
obtained some additional evidence from a sailor blown off his 
course who claimed to have reached land in the west and 
returned, (c) he met great difficulties in getting someone to 
provide the money to enable him to test his idea as well as in the 
actual carrying out of the experimental voyage, (d) when finally 
he succeeded he did not find the expected new route, but instead 
found a whole new world, ( e ) despite all evidence to the contrary 
he clung to the bitter end to his hypothesis and beheved that he 
had found the route to the Orient, (/) he got little credit or 
reward during his lifetime and neither he nor others realised the 
full implications of his discovery, (g) since his time evidence 
has been brought forward showing that he was by no means the 
first European to reach America. 

In his early investigations on diphtheria, Loffler showed that 
in experimental animals dying after inoculation with the diph- 
theria bacillus, the bacteria remained localised at the site of 
injection. He suggested that death was caused by toxin produced 
by the bacteria. Following this hypothesis, Emile Roux made 
numerous experiments attempting to demonstrate such a toxin 
in cultures of bacteria, but, try as he might, he could not 



demonstrate it. However, he persisted in his conviction and 
finally in desperation he injected the heroic dose of 35 ml. of 
culture filtrate into a guinea-pig. Rather surprisingly the guinea- 
pig survived the injection of this volume of fluid and in due 
course Roux had the satisfaction of seeing the animal die with 
lesions of diphtheria intoxication. Having established this point 
Roux was soon able to find out that his difficulties were due 
to the cultures not having been incubated long enough to 
produce much toxin, and by prolonged incubation he was able 
to produce powerfully toxic filtrates. This discovery led to 
immunisation against diphtheria and the therapeutic use of 

Following the hypothesis that impulses pass along sympathetic 
nerves and set up chemical changes producing heat in the skin, 
Claude Bernard severed the cervical sympathetic nerve in the 
expectation of it leading to cooling of the rabbit's ear. To his 
surprise the ear on that side became warmer. He had disconnected 
the blood vessels of the ear from the nervous influence which 
normally holds them moderately contracted, resulting in a 
greater flow of blood and hence warming of the ear. Without 
at first realising what he had done, he had stumbled on to the 
fact that the flow of blood through the arteries is controlled by 
nerves, one of the most important advances in knowledge of 
circulation since Harvey's classical discovery. An interesting and 
important illustration of what often happens in the field of 
observation is provided by Bernard's statement that from 1841 
onwards he had repeatedly divided the cervical sympathetic 
without observing these phenomena which he saw for the first 
time in 1851. In the previous experiments his attention was 
directed to the pupil; it was not till he looked for changes in the 
face and ear that he saw them.^* 

Claude Bernard reasoned that the secretion of sugar by the 
liver would be controlled by the appropriate nerve, which he 
supposed was the vagus. Therefore he tried puncturing the origin 
of the nerve in the floor of the fourth ventricle, and found 
that the glycogenic function of the liver was greatly increased 
and the blood sugar rose to such an extent that sugar appeared 
in the urine. However, Bernard soon realised that, interesting 
and important as were the results obtained, the hypothesis on 



which the experiment was founded was quite false because 
this effect was still obtained even after the vagus had been 
severed. He again showed his capacity to abandon the original 
reasoning and followed the new clue. In telling this story he 
said : 

"We must never be too absorbed by the thought we are 

This investigation has also interest from another point of view. 
After his first success in producing diabetes by puncturing the 
fourth ventricle he had great trouble in repeating it and only 
succeeded after he had ascertained the exact technique necessary. 
He was indeed fortunate in succeeding in the first attempt, for 
otherwise after faiUng two or three times he would have aban- 
doned the idea. 

** We wish to draw from this experiment another general 
conclusion . . . negative facts when considered alone never teach 
us anything. How often must man have been and still must be 
wrong in this way? It even seems impossible absolutely to avoid 
this kind of mistake." ^^ 

Towards the end of the last century nothing was known about 
the nature and cause of the condition in cows known as milk 
fever. There was no treatment of any value, and many valuable 
animals died of it. A veterinarian named Schmidt in Kolding, 
Denmark, formed an hypothesis that it was an auto-intoxication 
due to absorption of "colostrum corpuscles and degenerated 
old epithelial cells" from the udder. So, with the object of 
"checking the formation of colostral milk and paralysing any 
existing poison" he treated cases by injecting a solution of 
potassium iodide into the udder. At first he said that a small 
amount of air entering the udder during the operation was 
beneficial because it helped the Hberation of free iodine. The 
treatment was strikingly successful. Later he regarded the 
injection of copious amounts of air along with the solution as an 
important part of the treatment, on the ground that the air 
made it possible to massage the solution into all parts of the 
udder. The treatment was adopted widely and modified in 
various ways and soon it was found that the injection of air 
alone was quite as effective. This treatment based on a false idea 



became standard practice twenty-five years before the bio- 
chemical processes involved in milk fever were elucidated; 
indeed the basic cause of the disease is still not understood, 
nor do we know why the injection of air usually cures the 
disease/'* *^ 

An hypothesis may be fruitful, not only for its propounder, 
but may lead to developments by others. Wassermann himself 
testified that his discovery of the complement fixation test for 
syphilis was only made possible by EhrUch's side-chain theory. 
Also the development of the Wassermann test has another 
interesting aspect. Since it was not possible to obtain a culture 
of the spirochaete which causes syphilis, he used as antigen 
an extract of liver of syphiHtic stillborn children, which he 
knew contained large numbers of spirochaetes. This worked very 
well and it was not until some time later that it was found that 
not only was it unnecessary to use syphilitic hver but equally 
good antigens could be prepared from normal organs of other 
animals. To this day it is a mystery why these antigens give a 
complement fixation reaction which can be used to diagnose 
syphilis, and only one thing is certain : that the idea that 
prompted Wassermann to use an extract of liver was entirely 
fortuitous. But since we still see no reasoned explanation, we 
would probably still have no serological test for syphilis but for 
Wasserman's false but fruitful idea. 

The foundation of chemotherapy was due to Paul Ehrlich's 
idea that, since some dyes selectively stained bacteria and 
protozoa, substances might be found which could be selectively 
absorbed by the parasites and kill them without damaging the 
host. His faith in this idea enabled him to persist in the face 
of long continued frustration, repeated failure and attempts by 
his friends to dissuade him from the apparently hopeless task. 
He met with no success until he found that trypan red had some 
activity against protozoa and, developing further along lines 
suggested by this, he later developed salvarsan, an arsenical 
compound effective therapeutically against syphiHs, the six hun- 
dred and sixth compound of the series. This is perhaps the 
best example in the history of the study of disease of faith 
in a hypothesis triumphing over seemingly insuperable difficulties. 
It would be satisfying to end the story there but, as so often 



happens, in science, the final note must be one of irony. Ehrhch's 
search for substances which are selectively absorbed by patho- 
genic organisms was inspired by his firm belief that drugs cannot 
act unless fixed to the organisms; but to-day many effective 
chemotherapeutic drugs are known not to be selectively fixed to 
the infective agents. 

However the story is not yet finished. Gerhard Domagk, 
impressed by Ehrlich's early work, tried the effects of a great 
number of dyes belonging to the group called " azo-dyes " to 
which Ehrlich's trypan red belonged. Then in 1932 he found a 
dye of this series, prontosil, which was effective therapeutically 
against streptococci without damaging the infected animal. This 
discovery marked the beginning of a new era in medicine. But 
when the French chemist, Trefouel, set to work on the composi- 
tion of the drug he was amazed to find its action was in no 
way due to the fact that it was a dye, but was due to it con- 
taining sulphanilamide, which is not a dye. Again Ehrlich's 
false idea had led to a discovery that can justly be described as 
miraculous. Sulphanilamide had been known to chemists since 
1 9 08 but no one had any reason to suspect it had therapeutic 
properties. It has been said that, had its properties been known, 
sulphanilamide could have saved 750,000 lives in the 191 4-18 
war alone.* Ehrlich's early work with dyes is said also to be the 
starting point of the work which led to the discovery of the 
modern anti-malarial drug atebrin without which the Allies might 
not have won the war in the Pacific. 

Another group of chemotherapeutic substances which were 
evolved by following an hypothesis is the diamidine group used 
against the leishmania v.'hich causes kala-azar. The idea with 
which the investigation was started off was to interfere with the 
natural metabolic processes of the parasite, especially with its 
glucose metabolism, by using certain derivatives of insulin. One 
of these, synthalin, was found to have a remarkable leish- 
manicidal action, but in a dilution far higher than could possibly 
affect glucose metabolism. Thus, although the hypothesis was 
wrong, it led to the discovery of a new group of useful 

In certain parts of Great Britain and Western Australia there 
occurs a nervous disease of sheep known as swayback, the cause 



of which baffled investigators for years. In Western Australia, 
H. W. Bennetts for certain reasons suspected that the disease 
might be due to lead intoxication. To test this hypothesis he 
treated some sheep with ammonium chloride which is the 
antidote to lead. The first trial with this gave promising results, 
which, however, were not borne out by subsequent trials. This 
suggested that the disease might be due to the deficiency of some 
mineral which was present in small amounts in the first batch 
of ammonium chloride. Following up this clue, Bennetts was 
soon able to show that the disease was due to deficiency of copper, 
a deficiency never previously known to produce disease in any 
animal. In Bennetts' own words : 

" The solution of the etiology came in Western Australia from 
an accidental ' lead ' [clue] resulting from the testing of a false 

Use of hypothesis in research 

Hypothesis is the most important mental technique of the 
investigator, and its main function is to suggest new experiments 
or new observations. Indeed, most experiments and many 
observations are carried out with the deliberate object of 
testing an hypothesis. Another function is to help one see the 
significance of an object or event that otherwise would mean 
nothing. For instance, a mind prepared by the hypothesis of 
evolution would make many more significant observations on a 
field excursion than one not so prepared. Hypotheses should be 
used as tools to uncover new facts rather than as ends in 

The illustrations given above show some of the ways in which 
hypotheses lead to discoveries. The first thing that arrests 
attention is the curious and interesting fact that an hypothesis 
is sometimes very fruitful without being correct — a point that 
did not escape the attention of Francis Bacon. Several of the 
illustrations have been selected as striking demonstrations of 
this point, and it should not be thought that they are a truly 
representative sample, for correct guesses are more hkely to be 
productive than ones that are wrong, and the fact that the 
latter are sometimes useful does not detract from the importance 
of striving for correct explanations. The examples are, however, 



realistic in that the vast majority of hypotheses prove to be 

When the results of the first experiment or set of observations 
are in accord with expectations, the experimenter usually still 
needs to seek further experimental evidence before he can place 
much confidence in his idea. Even when confirmed by a number 
of experiments, the hypothesis has been established as true only 
for the particular circumstances prevailing in the experiments. 
Sometimes this is all the experimenter claims or requires for he 
now has a solution of the immediate problem or a working 
hypothesis on which to plan further investigation of that 
problem. At other times the value of the hypothesis is as a 
base from which new lines of investigation branch out in various 
directions, and it is appHed to as many particular cases as 
possible. If the hypothesis holds good under all circumstances, 
it may be elevated to the category of a theory or even, if 
sufficiently profound, a "law". An hypothesis which is a 
generalisation cannot, however, be absolutely proved, as is 
explained in the chapter on Reason ; but in practice it is accepted 
if it has withstood a critical testing, especially if it is in accord 
with general scientific theory. 

When the results of the first experiment or observation fail 
to support the hypothesis, instead of abandoning it altogether, 
sometimes the contrary facts are fitted in by a subsidiary clarify- 
ing hypothesis. This process of modification may go on till 
the main hypothesis becomes ridiculously overburdened with 
ad hoc additions. The point at which this stage is reached is 
largely a matter of personal judgment or taste. The whole 
edifice is then broken down and supplanted by another that 
makes a more acceptable synthesis of all the facts now available. 

There is an interesting saying that no one believes an hypo- 
thesis except its originator but everyone believes an experiment 
except the experimenter. Most people are ready to believe 
something based on experiment but the experimenter knows 
the many little things that could have gone wrong in the 
experiment. For this reason the discoverer of a new fact seldom 
feels quite so confident of it as do others. On the other hand 
other people are usually critical of an hypothesis, whereas the 
originator identifies himself with it and is liable to become 



devoted to it. It is as well to remember this when criticising 
someone's suggestion, because you may offend and discourage 
him if you scorn the idea. A corollary to this observation that 
an hypothesis is a very personal matter, is that a scientist usually 
works much better when pursuing his own than that of someone 
else. It is the originator who gets both the personal satisfaction 
and most of the credit if his idea is proved correct, even if he 
does not do the work himself A man working on an hypothesis 
which is not his own often abandons it after one or two 
unsuccessful attempts because he lacks the strong desire to con- 
firm it which is necessary to drive him to give it a thorough trial 
and think out all possible ways of varying the conditions of 
the experiment. Knowing this, the tactful director of research 
tries to lead the worker himself to suggest the line of work 
and then lets him feel the idea was his. 

Precautions in the use of hypothesis 

(a) Not to cling to ideas proved useless. Hypothesis is a tool 
which can cause trouble if not used properly. We must be 
ready to abandon or modify our hypothesis as soon as it is shown 
to be inconsistent with the facts. This is not as easy as it sounds. 
When delighted by the way one's beautiful brain-child seems to 
explain several otherwise incongruous facts and offers promise 
of further advances, it is tempting to overlook an observation 
that does not fit into the pattern woven, or to try to explain 
it away. It is not at all rare for investigators to adhere to their 
broken hypotheses, turning a blind eye to contrary evidence, 
and not altogether unknown for them deliberately to suppress 
contrary results. If the experimental results or observations are 
definitely opposed to the hypothesis or if they necessitate unduly 
complicated or improbable subsidiary hypotheses to accom- 
modate them, one has to discard the idea with as few regrets 
as possible. It is easier to drop the old hypothesis if one can 
find a new one to replace it. The feeling of disappointment too 
will then vanish. 

It was characteristic of both Darwin and Bernard that they 
were ready to drop or modify their hypotheses as soon as they 
ceased to be supported by the facts observed. The scientist who 
has a fertile mind and is rich in ideas does not find it so difficult 



to abandon one found to be unsatisfactory as does the man 
who has few. It is the latter who is most in danger of wasting 
time in hanging on to a notion after the facts warrant its 
discard. Zinsser picturesquely refers to people clinging to sterile 
ideas as resembling hens sitting on boiled eggs. 

On the other hand, faith in the hypothesis and perseverance 
is sometimes very desirable, as shown by the examples quoted 
concerning Roux and Ehrlich. Similarly Faraday persisted with 
his idea in the face of repeated failures before he finally succeeded 
in producing electric current by means of a magnet. As Bernard 
observed, negative results mean very little. There is a great 
difference between (a) stubborn adherence to an idea which is 
not tenable in face of contrary evidence, and (b) persevering 
with an hypothesis which is very difficult to demonstrate but 
against which there is no direct evidence. The investigator must 
judge the case with ruthless impartiality. However, even when 
the facts fit into the second category^ there may come a time 
when if no progress is being made it is wisest to abandon the 
attempt, at least temporarily. The hypothesis may be perfectly 
good but the techniques or knowledge in related fields required 
for its verification may not yet be available. Sometimes a project 
is put on one side for years and taken up again when fresh 
knowledge is available or the scientist has thought of a new 

(b) Intellectual discipline of subordinating ideas to facts. A 
danger constantly to be guarded against is that as soon as one 
formulates an hypothesis, parental aflfection tends to influence 
observations, interpretation and judgment; "wishful thinking" 
is likely to start unconsciously. Claude Bernard said : 

" Men who have excessive faith in their theories or ideas are 
not only ill-prepared for making discoveries; they also make poor 

Unless observations and experiments are carried out with 
safeguards ensuring objectivity, the results may unconsciously 
be biased. No less an investigator than Gregor Mendel seems 
to have fallen into this trap, for Fisher^* has shown that his 
results were biased in favour of his expectations. The German 
zoologist, Gatke, was so convinced of the truth of his views on 
the high speed that birds are capable of that he reported actual 



observations of birds covering four miles in a minute. He is 
believed to have been quite sincere but allowed his beliefs to 
delude him into making false observations/^ 

The best protection against these tendencies is to cultivate an 
intellectual habit of subordinating one's opinions and wishes to 
objective evidence and a reverence for things as they really are, 
and to keep constantly in mind that the hypothesis is only a 
supposition. As Thomas Huxley so eloquently said : 

" My business is to teach my aspirations to conform themselves 
to fact, not to try to make facts harmonise with my aspirations. 
Sit down before fact as a little child, be prepared to give up 
every preconceived notion, follow humbly wherever nature leads, 
or you will learn nothing." 

An interesting safeguard has been suggested by Chamberlain,^* 
namely, the principle of multiple hypotheses in research. His 
idea was that as many hypotheses as possible should be invented 
and all kept in mind during the investigation. This state of 
mind should prompt the observer to look for facts relative to 
each and may endow otherwise trivial facts with significance. 
However, I doubt if this method is often practicable. The 
more usual practice is a succession of hypotheses, selecting the 
most likely one for trial, and, if it is found wanting, passing on 
to another. 

When Darwin came across data unfavourable to his hypothesis, 
he made a special note of them because he knew they had a way 
of slipping out of the memory more readily than the welcome 

(c) Examining ideas critically. One should not be too ready 
to embrace a conjecture that comes into the mind; it must be 
submitted to most careful scrutiny before being accepted even 
as a tentative hypothesis, for once an opinion has been formed 
it is more difficult to think of alternatives. The main danger 
lies in the idea that seems so " obvious " that it is accepted 
almost without question. It seemed quite reasonable, in cases of 
cirrhosis of the liver, to rest that organ as much as possible by 
giving a low protein diet, but recent investigations have shown 
that this is just what should not be done, for low protein diet 
can itself cause liver damage. The practice of resting sprained 



joints was questioned by no one until a few years ago when a 
bold spirit found they got better much quicker under a regimen 
of exercise. For many years farmers practised keeping the surface 
of the soil loose as a mulch, believing this to decrease the loss of 
water by evaporation. B. A. Keen showed that this beHef was 
based on inadequate experiments and that under most circum- 
stances the practice was useless. He thus saved the community 
from a great deal of useless expenditure. 

(d) Shunning misconceptions. Examples have been quoted 
showing how hypotheses may be fruitful even when wrong, but 
nevertheless the great majority have to be abandoned as useless. 
More serious is the fact that false hypotheses or concepts some- 
times survive which, far from being productive, are actually 
responsible for holding up the advance of science. Two 
examples are the old notion that every metal contains mercury, 
and the phlogiston doctrine. According to the latter, every 
combustible substance contains a constituent which is given up 
on burning, called phlogiston. This notion for long held up the 
advance of chemistry, and stood in the way of an understanding 
of combustion, oxidation, reduction, and other processes. It 
was finally exposed as a fallacy by Lavoisier in 1778, but the 
great English scientists, Priestley, Watt and Cavendish, clung to 
the belief for some time afterwards and Priestley had not been 
converted to the new outlook when he died in 1804. 

The exposure of serious fallacies can be as valuable in the 
advance of science as creative discoveries, Pasteur fought and 
conquered the notion of spontaneous generation and Hopkins 
the semi-mystical concept of protoplasm as a giant molecule. 
Misconceptions in medicine, apart from holding up advances, 
have been the cause of much harm and unnecessary suffering. 
For example, the famous Philadelphian physician, Benjamin 
Rush (i 745-181 3), gave as an instance of the sort of treatment 
he meted out : 

"From a newly arrived Englishman I took 144 ounces at 12 
bleedings in 6 days; four were in 24 hours; I gave within the 
course of the same 6 days nearly 150 grains of calomel with the 
usual proportions of jalop and gamboge." 

' 66 

Once ideas have gained credence, they are rarely abandoned 



merely because some contrary facts are found. False ideas are 
only dropped when hypotheses more in accord with the new 
facts are put forward. 


The hypothesis is the principal intellectual instrument in 
research. Its function is to indicate new experiments and 
observations and it therefore sometimes leads to discoveries even 
when not correct itself 

We must resist the temptation to become too attached to 
our hypothesis, and strive to judge it objectively and modify 
or discard it as soon as contrary evidence is brought to light. 
Vigilance is needed to prevent our observations and interpreta- 
tions being biased in favour of the hypothesis. Suppositions can 
be used without being believed. 




" With accurate experiment and observation to work upon, 
imagination becomes the architect of physical theory." 

— Tyndall 

Productive thinking 

THIS chapter and the next contain a brief discussion on 
how ideas originate in the mind and what conditions are 
favourable for creative mental eflfort. The critical examination 
of the processes involved will be rendered easier if I do as I 
have done in other parts of this book, and make an arbitrary 
division of what is really a single subject. Consequently much 
of the material in this chapter should be considered in connection 
with Intuition and much of the next chapter appUes equally to 

Dewey analyses conscious thinking into the following phases. 
First comes awareness of some difficulty or problem which 
provides the stimulus. This is followed by a suggested solution 
springing into the conscious mind. Only then does reason come 
into play to examine and reject or accept the idea. If the idea 
is rejected, our mind reverts to the previous stage and the 
process is repeated. The important thing to realise is that the 
conjuring up of the idea is not a dehberate, voluntary act. It 
is something that happens to us rather than something we do.^' 

In ordinary thinking ideas continually " occur " to us in this 
fashion to bridge over the steps in reasoning and we are so 
accustomed to the process that we are hardly aware of it. Usually 
the new ideas and combinations result from the immediately pre- 
ceding thought calling up associations that have been developed 
in the mind by past experience and education. Occasionally, how- 
ever, there flashes into the mind some strikingly original idea, not 
based on past associations or at any rate not on associations that 
are at first apparent. We may suddenly perceive for the first time 



the connection between several things or ideas, or may take a 
great leap forward instead of the usual short step where the 
connections between each pair or set of ideas are well established 
and " obvious ". These sudden, large progressions occur not 
only when one is consciously puzzling the problem but also not 
uncommonly when one is not thinking of anything in particular, 
or even when one is mildly occupied with something different, 
and in these circumstances they are often startling. Although 
there is probably no fundamental difference between these ideas 
and the less exciting ones that come to us almost continually, 
and it is not possible to draw any sharp distinction, it will be 
convenient to consider them separately in the next chapter under 
the title " intuitions ".In this section we will draw attention to 
some general features of productive or creative thinking. 

Dewey advocates what he calls " reflective thinking ", that is, 
turning a subject over in the mind and giving it ordered and 
consecutive consideration, as distinct from the free coursing of 
ideas through the head. Perhaps the best term for the latter 
is day-dreaming; it also has its uses, as we shall see presently. 
But thinking may be reflective and yet be inefficient. The thinker 
may not be sufficiently critical of ideas as they arise and may 
be too ready to jump to a conclusion, either through impatience 
or laziness. Dewey says many people will not tolerate a state of 
doubt, either because they will not endure the mental discomfort 
of it or because they regard it as evidence of inferiority. 

" To be genuinely thoughtful, we must be willing to sustain 
and protract that state of doubt which is the stimulus to thorough 
enquiry, so as not to accept an idea or make a positive assertion 
of a belief, until justifying reasons have been found."^^ 

Probably the main characteristic of the trained thinker is that 
he does not jump to conclusions on insufficient evidence as the 
untrained man is inclined to do. 

It is not possible deliberately to create ideas or to control their 
creation. When a difficulty stimulates the mind, suggested 
solutions just automatically spring into the consciousness. The 
variety and quaUty of the suggestions are functions of how well 
prepared our mind is by past experience and education pertinent 
to the particular problem. What we can do deliberately is to 
prepare our minds in this way, voluntarily direct our thoughts 



to a certain problem, hold attention on that problem and appraise 
the various suggestions thrown up by the subconscious mind. 
The intellectual element in thinking is, Dewey says, what we do 
with the suggestions after they arise. 

Other things being equal, the greater our store of knowledge, 
the more likely it is that significant combinations will be thrown 
up. Furthermore, original combinations are more likely to come 
into being if there is available a breadth of knowledge extend- 
ing into related or even distant branches of knowledge. As 
Dr. E. L. Taylor says : 

" New associations and fresh ideas are more likely to come 
out of a varied store of memories and experience than out of 
a collection that is all of one kind." ^"^ 

Scientists who have made important original contributions 
have often had wide interests or have taken up the study of a 
subject different from the one in which they were originally 
trained. Originahty often consists in finding connections or 
analogies between two or more objects or ideas not previously 
shown to have any bearing on each other. 

In seeking original ideas, it is sometimes useful to abandon 
the directed, controlled thinking advocated by Dewey and allow 
one's imagination to wander freely — to day-dream. Harding 
says all creative thinkers are dreamers. She defines dreaming in 
these words : 

" Dreaming over a subject is simply . . . allowing the will to 
focus the mind passively on the subject so that it follows the 
trains of thought as they arise, stopping them only when unprofit- 
able but in general allowing them to form and branch naturally 
until some useful and interesting results occur." ^^ 

Max Planck said : 

" Again and again the imaginary plan on which one attempts 
to build up order breaks down and then we must try another. 
This imaginative vision and faith in the ultimate success are 
indispensable. The pure rationalist has no place here."^° 

In meditating thus, many people find that visualising the 
thoughts, forming mental images, stimulates the imagination. It 
is said that Clerk Maxwell developed the habit of making a 
mental picture of every problem. Paul Ehrlich was another 
great advocate of making pictorial representations of ideas, as 



\''<:^^'j '-~'' 


one can see from his illustrations of his side-chain theory. 
Pictorial analogy can play an important part in scientific think- 
ing. This is how the German chemist Kekule hit on the concep- 
tion of the benzene ring, an idea that revolutionised organic 
chemistry. He related how he was sitting writing his chemical 
text-book : 

" But it did not go well; my spirit was with other things. I 
turned the chair to the fireplace and sank into a half sleep. The 
atoms flitted before my eyes. Long rows, variously, more closely, 
united; all in movement wriggling and turning like snakes. And 
see, what was that? One of the snakes seized its own tail and 
the image whirled scornfully before my eyes. As though from a 
flash of lightning I awoke; I occupied the rest of the night in 
working out the consequences of the hypothesis. . . . Let us 
learn to dream, gentlemen."^* 

However, physics has reached a stage where it is no longer 
possible to visualise mechanical analogies representing certain 



phenomena which can only be expressed in mathematical terms. 

In the study of infectious diseases, it is sometimes helpful 
to take the biological view, as Burnet has done, and look upon 
the causal organism as a species struggling for continued survival, 
or even, as Zinsser has felt inclined to do with typhus, which he 
spent a lifetime studying, personifying the disease in the 

An important inducement to seeking generalisations, especially 
in physics and mathematics, is the love of order and logical 
connection between facts. Einstein said : i 

" There is no logical way to the discovery of these elemental 
laws. There is only die way of intuition, which is helped by a 
feeling for the order lying behind the appearance." ^^ 

W. H. George remarks that a feeling of tension is produced 
when an observer sees the objects lying in his field of vision as 
forming a pattern with a gap in it, and a feeling of relaxation 
or satisfaction is experienced when the gap is closed, and all 
parts of the pattern fit into their expected places. Generalisa- 
tions may be regarded as patterns in ideas.^^ Another 
phenomenon which may be explained by this concept is the 
satisfaction experienced on the completion of any task. This 
may be quite rnassociated with any consideration of reward 
for it applies equally to unimportant, self-appointed tasks such 
as doing a crossword puzzle, climbing a hill or reading a book. 
The instinctive sense of irritation we feel when someone disagrees 
with us or when some fact arises which is contrary to our 
beliefs may be due to the break in the pattern we have formed. 

The tendency of the human mind to seek order in things did 
not escape the penetrating intelligence of Francis Bacon. He 
warned against the danger that this trait may mislead us into 
believing we see a greater degree of order and equality than there 
really is. 

When one has succeeded in hitting upon a new idea, it has 
to be judged. Reason based on knowledge is usually sufficient 
in everyday affairs and in straightforward matters in science, 
but in research there is often insufficient information available 
for effective reasoning. Here one has to fall back on " feelings " 
or " taste ". Harding says : 



*' If the scientist has during the whole of his Hfe observed 
carefully, trained himself to be on the look out for analogy, and 
possessed himself of relevant knowledge, then the ' instrument of 
feeling ' . . . will become a powerful divining rod ... in creative 
science feeling plays a leading part."^^ 

Writing of the importance of imagination in science Tyndall 
said : 

" Newton's passage from a falling apple to a falling moon was 
an act of the prepared imagination. Out of the facts of chemistry 
the constructive imagination of Dalton formed the atomic theory. 
Davy was richly endowed with the imaginative faculty, while 
with Faraday its exercise was incessant, preceding, accompanying 
and guiding all his experiments. His strength and fertility as a 
discoverer are to be referred in great part to the stimulus of 
the imagination."^^ 

Imagination is of great importance not only in leading us 
to new^ facts, but also in stimulating us to new efforts, for it 
enable us to see visions of their possible consequences. Facts 
and ideas are dead in themselves and it is the imagination that 
gives hfe to them. But dreams and speculations are idle fantasies 
unless reason turns them to useful purpose. Vague ideas captured 
on flights of fancy have to be reduced to specific propositions 
and hypotheses. 

False trails 

While imagination is the source of inspiration in seeking new 
knowledge, it can also be dangerous if not subjected to discipline; 
a fertile imagination needs to be balanced by criticism and judg- 
ment. This is, of course, quite different from saying it should be 
repressed or crushed. The imagination merely enables us to 
wander into the darkness of the unknown where, by the dim 
light of the knowledge that we carry, we may glimpse something 
that seems of interest. But when we bring it out and examine 
it more closely it usually proves to be only trash whose glitter 
had caught our attention. Things not clearly seen often take on 
grotesque forms. Imagination is at once the source of all hope 
and inspiration but also of frustration. To forget this is to court 

Most hypotheses prove to be wrong whatever their origin may 
be. Faraday wrote : 



" The world little knows how many of the thoughts and 
theories which have' passed through the mind of a scientific 
investigator have been crushed in silence and secrecy by his own 
severe criticism and adverse examinations; that in the most 
successful instances not a tenth of the suggestions, the hopes, 
the wishes, the preliminary conclusions have been realised." 

Every experienced research worker will confirm this statement. 
Darwin went even further : 

" I have steadily endeavoured to keep my mind free so as to 
give up any hypothesis, however much beloved (and I cannot 
resist forming one on every subject) as soon as facts are shown 
to be opposed to it. ... / cannot remember a single first formed 
hypothesis which had not after a time to he given up or be 
greatly modified." -^ (Italics mine.) 

T. H. Huxley said that the great tragedies of science are the 
slaying of beautiful hypotheses by ugly facts. F. M. Burnet has 
told me that most of the "bright ideas" that he gets prove 
to be wrong. 

There is nothing reprehensible about making a mistake, 
provided it is detected in time and corrected. The scientist who 
is excessively cautious is not likely to make either errors or 
discoveries. Whitehead has expressed this aptly : " panic of 
error is the death of progress." Humphrey Davy said : " The 
most important of my discoveries have been suggested to me 
by my failures." The trained thinker shows to great advantage 
over the untrained person in his reaction to finding his idea to 
be wrong. The former profits from his mistakes as much as 
from his successes. Dewey says : 

" What merely annoys and discourages a person not accus- 
tomed to thinking ... is a stimulus and guide to the trained 
enquirer. ... It either brings to light a new problem or helps to 
define and clarify the problem." ^^ 

The productive research worker is usually one who is not 
afraid to venture and risk going astray, but who makes a rigorous 
test for error before reporting his findings. This is so not only 
in the biological sciences but also in mathematics. Hadamard 
states that good mathematicians often make errors but soon 
perceive and correct them, and that he himself makes more 
errors than his students. Commenting on this statement, Sir 



Frederic Bartlett, Professor of Psychology at Cambridge, suggests 
that the best single measure of mental skill may lie in the speed 
with which errors are detected and thrown out/^ Lister once 
remarked : 

" Next to the promulgation of the truth, the best thing I can 
conceive that a man can do is the public recantation of an error." 

W. H. George points out that even with men of genius, with 
whom the birth rate of hypotheses is very high, it only just 
manages to exceed the death rate. 

Max Planck, whose quantum theory is considered by many 
to be an even more important contribution to science than 
Einstein's theory of relativity, said when he was awarded the 
Nobel Prize : 

" Looking back . . . over the long and labyrinthine path 
which finally led to the discovery [of the quantum theory], I 
am vividly reminded of Goethe's saying that men will always be 
making mistakes as long as they are striving after something."^" 

Einstein in speaking of the origin of his general theory of 
relativity said : 

" These were errors in thinking which caused me two years 
of hard work before at last, in 1915, I recognised them as such. 
. . . The final results appear almost simple; any intelligent under- 
graduate can understand them without much trouble. But the 
years of searching in the dark for a truth that one feels, but 
cannot express; the intense desire and the alternations of confi- 
dence and misgiving, until one breaks through to clarity and 
understanding, are only known to him who has himself experi- 
enced them."^^ 

Perhaps the most interesting and revealing anecdote on these 
matters was written by Hermann von Helmholtz^^ : 

"In 1 89 1 I have been able to solve a few problems in mathe- 
matics and physics including some that the great mathematicians 
had puzzled over in vain from Euler onwards. . . . But any pride 
I might have felt in my conclusions was perceptibly lessened by 
the fact that I knew that the solution of these problems had 
almost always come to me as the gradual generalisation of favour- 
able examples, by a series of fortunate conjectures, after many 
errors. I am fain to compare myself with a wanderer on the 
mountains who, not knowing the path, climbs slowly and pain- 
fully upwards and often has to retrace his steps because he can 



go no further — then, whether by taking thought or from luck, 
discovers a new track that leads him on a little till at length 
when he reaches the summit he finds to his shame that there is 
a royal road, by which he might have ascended, had he only had 
the wits to find the right approach to it. In my works, I naturally 
said nothing about my mistake to the reader, but only described 
the made track by which he may now reach the same heights 
without difiiculty." 

Curiosity as an incentive to thinking 

In common with other animals we are bom with an instinct 
of curiosity. It provides the incentive for the young to discover 
the world in which they live — what is hard or soft, movable or 
fixed, that things fall downwards, that water has the property we 
call wetness, and all other knowledge required to enable us to 
accommodate ourselves to our environment. Infants whose 
mental reflexes have not yet been conditioned are said not to 
exhibit the " attack-escape " reaction as do adults, but to show 
rather the opposite type of behaviour. By school age we have 
usually passed this stage of development, and most of our 
acquisition of new knowledge is then made by learning from 
others, either by observing them or being told or reading. We 
have gained a working knowledge of our environment and our 
curiosity tends to become blunted unless it is successfully trans- 
ferred to intellectual interests. 

The curiosity of the scientist is usually directed toward seeking 
an understanding of things or relationships which he notices 
have no satisfactory explanation. Explanations usually consist 
in connecting new observations or ideas to accepted facts or 
ideas. An explanation may be a generalisation which ties together 
a bundle of data into an orderly whole that can be connected 
up with current knowledge and beliefs. That strong desire 
scientists usually have to seek underlying principles in masses of 
data not obviously related may be regarded as an adult form or 
sublimation of curiosity. The student attracted to research is 
usually one who retains more curiosity than usual. 

We have seen that the stimulus to the production of ideas is 
the awareness of a difificulty or problem, which may be the 
realisation of the present unsatisfactory state of knowledge. 
People with no curiosity seldom get this stimulus, for one usually 



becomes aware of the problem by asking why or how some 
process works, or something takes the form that it does. That 
a question is a stimulus is demonstrated by the fact that when 
someone asks a question it requires an effort to restrain oneself 
from responding. 

Some purists contend that scientists should wonder " how " 
and not " why ". They consider that to ask " why " implies that 
there is an intelligent purpose behind the design of things and 
that activities are directed by a supernatural agency toward 
certain aims. This is the teleological view and is rejected by 
present-day science, which strives to understand the mechanism 
of all natural phenomena. Von Bruecke once remarked : 

" Teleology is a lady without whom no biologist can live; yet 
he is ashamed to show himself in public with her." 

In biology, asking " why " is justified because all events have 
causes; and because structures and reactions usually fulfil some 
function which has survival value for the organism, and in that 
sense they have a purpose. Asking " why " is a useful stimulus 
towards imagining what the cause or purpose may be. " How " 
is also a useful question in provoking thought about the 
mechanism of a process. 

There is no satisfying the scientists' curiosity, for with each 
advance, as Pavlov said, " we reach a higher level from which 
a wider field of vision is open to us, and from which we see 
events previously out of range." It may be appropriate to give 
here an illustration of how curiosity led John Hunter to carry 
out an experiment which led to an important finding. 

While in Richmond Park one day Hunter saw a deer with 
growing antlers. He wondered what would happen if the blood 
supply were shut off on one side of the head. He carried out 
the experiment of tying the external carotid artery on one side, 
whereupon the corresponding antler lost its warmth and ceased 
to grow. But after a while the horn became warm again and 
grew. Hunter ascertained that his ligature still held, but neigh- 
bouring arteries had increased in size till they carried an adequate 
supply of blood. The existence of collateral circulation and the 
possibility of its increasing were thus discovered. Hitherto no 
one had dared to treat aneurism by ligation for fear of gangrene, 
but now Hunter saw the possibilities and tried ligation in the 



case of popliteal aneurism. So the Hunterian operation, as it is 
known in surgery to-day, came into an assured existence.^^ An 
insatiable curiosity seems to have been the driving force behind 
Hunter's prolific mind which laid the foundation of modem 
surgery. He even paid the expenses of a surgeon to go and 
observe whales for him in the Greenland fisheries. 

Discussion as a stimulus to the mind 

Productive mental effort is often helped by intellectual inter- 
course. Discussing a problem with colleagues or with lay 
persons may be helpful in one of several ways. 

(a) The other person may be able to contribute a useful 
suggestion. It is not often that he can help by directly indicating 
a solution of the impasse, because he is unlikely to have as 
much pertinent knowledge as has the scientist working on the 
problem, but with a different background of knowledge he may 
see the problem from a different aspect and suggest a new 
approach. Even a layman is sometimes able to make useful 
suggestions. For example, the introduction of agar for making 
solid media for bacteriology was due to a suggestion of the 
wife of Koch's colleague Hesse. ^* 

{h) A new idea may arise from the pooling of information 
or ideas of two or more persons. Neither of the scientists alone 
may have the information necessary to draw the inference which 
can be obtained by a combination of their knowledge. 

{c) Discussion provides a valuable means of uncovering errors. 
Ideas based on false information or questionable reasoning may 
be corrected by discussion and likewise unjustified enthusiasms 
may be checked and brought to a timely end. The isolated 
worker who is unable to talk over his work with colleagues will 
more often waste his time in following a false trail. 

[d) Discussion and exchange of views is usually refreshing, 
stimulating and encouraging, especially when one is in difficulties 
and worried. 

{e) The most valuable function of discussion is, I believe, to 
help one to escape from an established habit of thought which 
has proved fruitless, that is to say, from conditioned thinking. 
The phenomenon of conditioned thinking is discussed in the 
next section. 



Discussions need to be conducted in a spirit of helpfulness 
and mutual confidence and one should make a deliberate effort 
to keep an open receptive mind. Discussions are usually best 
when not more than about six are present. In such a group no 
one should be afraid of admitting his ignorance on certain 
matters and so having it corrected, for in these days of extreme 
specialisation everyone's knowledge is restricted. Conscious 
ignorance and intellectual honesty are important attributes for 
the research man. Free discussion requires an atmosphere 
unembarrassed by any suggestion of authority or even respect. 
Brailsford Robertson tells the story of the great biochemist, 
Jacques Loeb, who, when asked a question by a student after 
a lecture, replied characteristically : 

" I cannot answer your question, because I have not yet read 
that chapter in the text-book myself, but if you will come to me 
to-morrow I shall then have read it, and may be able to answer 

Students sometimes quite wrongly think that their teachers 
are almost omniscient, not knowing that the lecturers usually 
spend a considerable amount of time preparing their lectures, 
and that outside the topic of the lecture their knowledge is often 
much less impressive. Not only does the author of a text-book 
not carry in his head all the information in the book, but the 
author of a research paper not infrequently has to refer to the 
paper to recall the details of the work which he himself did. 

The custom of having lunch and afternoon tea in groups at 
the laboratory is a valuable one as it provides ample opportunities 
for these informal discussions. In addition, slightly more formal 
seminars or afternoon tea meetings at which workers present 
their problems before and during, as well as after, the investiga- 
tion are useful. Sharing of interests and problems among workers 
in a department or institute is also valuable in promoting a 
stimulating atmosphere in which to work. Enthusiasm is infectious 
and is the best safeguard against the doldrums. 

Conditioned thinking 

Psychologists have observed that once we have made an error, 
as for example in adding up a column of figures, we have a 



tendency to repeat it again and again. This phenomenon is known 
as the persistent error. The same thing happens when we ponder 
over a problem; each time our thoughts take a certain course, 
the more hkely is that course to be followed the next time. Asso- 
ciations form between the ideas in the chain of thoughts and 
become firmer each time they are used, until finally the connec- 
tions are so well established that the chain is very difficult to 
break. Thinking becomes conditioned just as conditioned reflexes 
are formed. We may have enough data to arrive at a solution to 
the problem, but, once we have adopted an unprofitable line of 
thought, the oftener we pursue it, the harder it is for us to 
adopt the profitable line. As Nicolle says, " The longer you are in 
the presence of a difficulty, the less likely you are to solve it." 

Thinking also becomes conditioned by learning from others 
by word of mouth or by reading. In the first chapter we discussed 
the adverse eflfect on originality of uncritical reading. Indeed, 
all learning is conditioning of the mind. Here, however, we are 
concerned with the eflfects of conditioning which are unprofitable 
for our immediate purpose, that of promoting original thought. 
This does not only concern learning or being conditioned to 
incorrect opinions for, as we have seen in the first chapter, read- 
ing, even the reading of what is true so far as it goes, may 
have an adverse effect on originality. 

The two main ways of freeing our thinking from conditioning 
are temporary abandonment and discussion. If we abandon a 
problem for a few days or weeks and then return to it the old 
thought associations are partly forgotten or less strong and often 
we can then see it in a fresh light, and new ideas arise. The 
beneficial eflfect of temporary abandonment is well shown by 
laying aside for a few weeks a paper one has written. On coming 
back to it, flaws are apparent that escaped attention before, 
and fresh pertinent remarks may spring into the mind. 

Discussion is a valuable aid in breaking away from sterile 
lines of thought that have become fixed. In explaining a prob- 
lem to another person, and especially to someone not familiar 
with that field of science, it is necessary to clarify and amplify 
aspects of it that have been taken for granted and the familiar 
chain of thought cannot be followed. Not infrequently it happens 
that while one is making the explanation, a new thought occurs 



to one without the other person having said a word. The same 
may happen during the delivery of a lecture, for when the 
teacher explains something he "sees" it more clearly himself 
than he had before. The other person, by asking questions, even 
ill-informed ones, may make the narrator break the established 
chain, even if only to explain the futiUty of the suggestion, and 
this may result in him seeing a new approach to the problem or 
the connection between two or more observations or ideas that 
he had not noticed before. The effect that questioning has on 
the mind might be Ukened to the stimulus given to a fire by 
poking ; it disturbs the settled arrangement and brings about new 
combinations. In disturbing fixed Hnes of thought, discussion is 
perhaps more likely to be helpful when carried on with someone 
not familiar with your field of work, for near colleagues have 
many of the same thought habits as yourself The writing of a 
review of the problem may prove helpful in the same way as 
the giving of a lecture. 

A further useful application of the conception of conditioned 
thinking is that when a problem has defied solution it is best 
to start again right from the beginning, and if possible with a 
new approach. For example, I worked unsuccessfully for several 
years trying to discover the micro-organism which causes foot-rot 
in sheep. I met with repeated frustrations but each time I started 
again along the same lines, namely, trying to select the causal 
organism by microscopy and then isolating it in culture. This 
method seemed the sensible one to follow and only when I had 
exhausted all possibilities and was forced to abandon it, did I 
think of a fundamentally different approach to the problem, 
namely, to try mixed cultures on various media until one was 
found which was capable of setting up the disease. Work along 
these lines soon led to the solution of the problem. 


Productive thinking is started off by awareness of a difficulty. 
A suggested solution springs into the mind and is accepted or 
rejected. New combinations in our thoughts arise from rational 
associations, or from fancy or perhaps chance circumstances. The 
fertile mind tries a large number and variety of combinations. 



The scientific thinker becomes accustomed to withholding judg- 
ment and remaining in doubt when the evidence is insufficient. 
Imagination only rarely leads one to a correct answer, and most 
of our ideas have to be discarded. Research workers ought not 
to be afraid of making mistakes provided they correct them in 
good time. 

Curiosity atrophies after childhood unless it is transferred to 
an intellectual plane. The research worker is usually a person 
whose curiosity is turned toward seeking explanations for pheno- 
mena that are not understood. 

Discussion is often helpful to productive thinking and informal 
daily discussion groups in research institutes are valuable. 

Once we have contemplated a set of data, the mind tends to 
follow the same line of thought each time and therefore unprofit- 
able lines of thought tend to be repeated. There are two aids to 
freeing our thought from this conditioning; to abandon the 
problem temporarily and to discuss it with another person, prefer- 
ably someone not familiar with our work. 




" The really valuable factor is intuition." — Albert Einstein 

Definition and illustration 

THE word intuition has several slightly different usages, so 
it is necessary to indicate at the outset that it is employed 
here as meaning a sudden enlightenment or comprehension of a 
situation, a clarifying idea which springs into the consciousness, 
often, though not necessarily, when one is not consciously think- 
ing of that subject. The terms inspiration, illumination and 
" hunch " are also used to describe this phenomenon but these 
words are very often given other meanings. Ideas coming drama- 
tically when one is not consciously thinking of the subject are 
the most striking examples of intuition, but those arriving 
suddenly when the problem is being consciously pondered are 
also intuitions. Usually these were not self-evident when the data 
were first obtained. All ideas, including the simple ones that 
form the gradual steps in ordinary reasoning, probably arise by 
the process of intuition and it is only for convenience that we 
consider separately in this chapter the more dramatic and import- 
ant progressions of thought. 

Valuable contributions on the subject of intuition in scientific 
thought have been made by the American chemists Piatt and 
Baker, ^^ by the French mathematicians Henri Poincare^^ and 
Jacques Hadamard,^" by W. B. Cannon,^^ the American physio- 
logist, and by Graham Wallas,^^ the psychologist. In writing this 
chapter I have drawn freely from the excellent article by Piatt 
and Baker who conducted an enquiry on the subject among 
chemists by questionnaire. The following illustrations are quoted 
from material collected by them. 

" Freeing my mind of all thoughts of the problem I walked 
briskly down the street, when suddenly at a definite spot which 





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I could locate to-day — as if from the clear sky above me — an idea 
popped into my head as emphatically as if a voice had shouted it." 

" I decided to abandon the work and all thoughts "relative to it, 
and then, on the following day, when occupied in work of an 
entirely different type, an idea came to my mind as suddenly as a 
flash of lightning and it was the solution . . . the utter simplicity 
made me wonder why I hadn't thought of it before." 

" The idea came with such a shock that I remember the exact 
position quite clearly.""^ 

Prince Kropotkin wrote : 

" Then followed months of intense thought in order to find 
out what the bewildering chaos of scattered observations meant 
until one dav all of a sudden the whole became as clear and 
comprehensible as if it were illuminated with a flash of light . . . 
There are not many joys in human life equal to the joy of the 
sudden birth of a generalisation illuminating the mind after a 
long period of patient research." 

Von Helmholtz, the great German physicist said that after 
previous investigation of a problem " in all directions . . . happy 
ideas came unexpectedly without effort like an inspiration." He 
found that ideas did not come to him when his mind was fatigued 
or when at the working table, but often in the morning after a 
night's rest or during the slow ascent of wooded hills on a 
sunny day. 

After Darwin had conceived the basic idea of evolution, he 
was reading Malthus on population for relaxation one day when 
it struck him that under the struggle for existence favourable 
variations would tend to be preserved and unfavourable ones 
destroyed. He wrote a memorandum around this idea, but there 
was still one important point not accounted for, namely, the 
tendency in organic beings descended from the same stock to 
diverge as they become modified. The clarification of this last 
point came to him under the following circumstances : 

" I can remember the very spot in the road, whilst in my 
carriage, when to my joy the solution occurred to me." 

The idea of survival of the fittest as a part of the explanation 
of evolution also came independently to A. R. Wallace when he 
was reading Malthus' Principles of Population during an illness. 



Malthus gave a clear exposition of the checks to increase in the 
human population and mentioned that these eliminated the least 
fit. Then it occurred to Wallace that the position was much the 
same in the animal world. 

" Vaguely thinking over the enormous and constant destruc- 
tion this implied, it occurred to me to ask the question, * Why 
do some die and some live? ' and the answer was clearly that on 
the whole the best fitted live. . . . Then it suddenly flashed upon 
me that this self-acting process would improve the race . . . 
the fittest would survive. Then at once I seemed to see the whole 
effect of this." ^^ 

Here is Metchnikoff's own account of the origin of the idea of 
phagocytosis : 

" One day when the whole family had gone to the circus to 
see some extraordinary performing apes, I remained alone with 
my microscope, observing the life in the mobile cells of a trans- 
parent starfish larva, when a new thought suddenly flashed across 
my brain. It struck me that similar cells might serve in the 
defence of the organism against intruders. Feeling that there was 
in this something of surpassing interest, I felt so excited that I 
began striding up and down the room and even went to the 
seashore to collect my thoughts." ^^ 

Poincare relates how after a period of intense mathematical 
work he went for a journey into the country and dismissed his 
work from mind. 

" Just as I put my foot on the step of the brake, the idea 
came to me . . . that the transformations I had used to define 
Fuchsian functions were identical with those of non-Euclidian 
geometry." ^^ 

On another occasion when baflfled by a problem he went to the 
seaside and 

" thought of entirely different things. One day, as I was walking 
on the cliff the idea came to me, again with the same character- 
istics of conciseness, suddenness and immediate certainty, that 
arithmetical transformations of indefinite ternary quadratic forms 
are identical with those of non-Euclidian geometry." 

Hadamard cites an experience of the mathematician Gauss, 
who wrote concerning a problem he had tried unsuccessfully to 
prove for years, 



" finally two days ago I succeeded . . . like a sudden flash of 
lightning the riddle happened to be solved. I cannot myself say 
what was the conducting thread which connected what I pre- 
viously knew with what made my success possible." 

Intuitions sometimes occur during sleep and a remarkable 
example is quoted by Cannon. Otto Loewi, professor of pharma- 
cology at the University of Graz, awoke one night with a brilliant 
idea. He reached for a pencil and paper and jotted down a few 
notes. On waking next morning he was aware of having had an 
inspiration during the night, but to his consternation could not 
decipher his notes. All day at the laboratory in the presence of 
familiar apparatus he tried to remember the idea and to decipher 
the note, but in vain. By bedtime he had been unable to recall 
anything, but during the night to his great joy he again awoke 
with the same flash of insight. This time he carefully recorded it 
before going to sleep again. 

" The next day he went to his laboratory and in one of the 
neatest, simplest and most definite experiments in the history of 
biology brought proof of the chemical mediation of nerve 
impulses. He prepared two frogs' hearts which were kept beating 
by means of salt solution. He stimulated the vagus nerve on 
one of the hearts, thus causing it to stop beating. He then 
removed the salt solution from this heart and applied it to the 
other one. To his great satisfaction the solution had the same 
effect on the second heart as the vagus stimulating had had on 
the first one: the pulsating muscle was brought to a standstill. 
This was the beginning of a host of investigations in many 
countries throughout the world on chemical intermediation, not 
only between nerves and the muscles and the glands they affect 
but also between nervous elements themselves." ^^ 

Cannon states that from his youth he was accustomed to get 
assistance from sudden and unpredicted insight and that not 
infrequently he would go to sleep with a problem on his mind 
and on waking in the morning the solution was at hand. The 
following passage shows a slightly different use of intuition. 

" As a matter of routine I have long trusted unconscious pro- 
cesses to serve me — for example, when I have had to prepare a 
public address. I would gather points for the address and write 



them down in rough outUne. Within the next few nights I would 
have sudden spells of awakening, with an onrush of illustrative 
instances, pertinent phrases, and fresh ideas related to those 
already listed. Paper and pencil at hand permitted the capture 
of these fleeting thoughts before they faded into oblivion. The 
process has been so common and so reliable for me that I have 
supposed that it was at the service of everyone. But evidence indi- 
cates that it is not." -^ 

Similarly, in preparing this book ideas have frequently come to 
me at odd times of the day, sometimes when I was thinking of 
it, sometimes when I was not. These were all jotted down and 
later sorted out. 

These examples should be ample to enable the reader to under- 
stand the particular sense in which I am using the word intuition 
and to realise its importance in creative thinking. 

Most but not all scientists are familiar with the phenomenon of 
intuition. Among those answering the questionnaire of Piatt and 
Baker 33 per cent reported frequent, 50 per cent occasional, and 
17 per cent no assistance from intuition. From other enquiries 
also it is known that some people, so far as they are aware, never 
get intuitions, or at any rate not striking ones. They have no com- 
prehension of what an intuition is, and believe that they derive 
their ideas only from conscious thinking. Some of these opinions 
may be based on insufhcient examination of the working of one's 
own mind. 

The examples cited may leave the reader with the impression 
that all intuitions are correct or at least fruitful, which, if so, 
would be inconsistent with what has been said about hypotheses 
and ideas in general. Unfortunately intuitions, being but the 
products of falUble human minds, are by no means always 
correct. In Piatt and Baker's enquiry, 7 per cent of scientists 
replying said their intuitions were always correct, and the 
remainder gave estimates varying from 10 per cent to 90 per 
cent of the intuitions as subsequently proving to be correct. 
Even this is probably an unduly favourable picture, because 
successful instances would tend to be remembered rather than 
the unsuccessful. Several eminent scientists have stated that most 
of their intuitions subsequently prove to be wrong and are 



Psychology of intuition 

The most characteristic circumstances of an intuition are a 
period of intense work on the problem accompanied by a desire 
for its solution, abandonment of the work perhaps with attention 
to something else, then the appearance of the idea with dramatic 
suddenness and often a sense of certainty. Often there is a feeUng 
of exhilaration and perhaps surprise that the idea had not been 
thought of previously. 

The psychology of the phenomenon is not thoroughly under- 
stood. There is a fairly general, though not universal, agreement 
that intuitions arise from the subconscious activities of the mind 
which has continued to turn over the problem even though 
perhaps consciously the mind is no longer giving it attention. 

In the previous chapter it was pointed out that ideas spring 
straight into the conscious mind without our having deliberately 
formed them. Evidently they originate from the subconscious 
activities of the mind which, when directed at a problem, 
immediately brings together various ideas which have been 
associated with that particular subject before. When a possibly 
significant combination is found it is presented to the cons<cious 
mind for appraisal. Intuitions coming w^hen we are consciously 
thinking about a problem are merely ideas that are more startling 
than usual. But some further explanation is needed to account for 
intuitions coming when our conscious mind is no longer dwelhng 
on that subject. The subconscious mind has probably continued 
to be occupied with the problem and has suddenly found a 
significant combination. Now, a new idea arriving during con- 
scious thinking often produces a certain emotional reaction — we 
feel pleased about it and perhaps somewhat excited. Perhaps the 
subconscious mind is also capable of reacting in this way and 
this has the eflfect of bringing the idea into the conscious mind. 
This is only a conjecture, but there can be Httle doubt that a 
problem may continue to occupy the subconscious mind, for 
common experience shows that sometimes you " can't get a 
problem off your mind " because it keeps cropping up involun- 
tarily in your thoughts. Secondly, there is no doubt about the 
emotion often associated with an intuition. 

Some ideas come into consciousness and are grasped, but might 
not some fail to appear in the conscious mind or only appear 



fleetingly and disappear again like the things we were about to 
say but slipped away irretrievably before there was a break in 
the conversation? According to the hypothesis just outlined the 
more emotion associated with the idea the more likely it would 
be to get through to the consciousness. On this reasoning one 
would expect it to be helpful to have a strong desire for a solution 
to the problem and also to cultivate a "taste" in scientific matters. 
It would be interesting to know whether scientists who say they 
never get intuitions are those who find no joy in new ideas or are 
deficient in emotional sensitivity. 

The conception of the psychology of intuition outlined is in 
accord with what is known about the conditions that are con- 
ducive to their occurrence. It provides an explanation for the 
importance of (a) freedom from other competing problems and 
worries, and {b) the helpfulness of periods of relaxation in 
allowing for the appearance of the intuition, for messages from 
the subconscious may not be received if the conscious mind is 
constantly occupied or too fatigued. There have been several 
instances of famous generalisations coming to people when they 
were ill in bed. The idea of natural selection in evolution came 
to Wallace during a bout of malaria, and Einstein has reported 
that his profound generalisation connecting space and time 
occurred to him while he was sick in bed. Both Cannon and 
Poincare report having got bright ideas when lying in bed unable 
to sleep — the only good thing to be said for insomnia ! It is said 
that James Brindley, the great engineer, when up against a 
difficult problem, would go to bed for several days till it was 
solved. Descartes is said to have made his discoveries while lying 
in bed in the morning and Cajal refers to those placid hours after 
awakening which Goethe and so many others considered pro- 
pitious to discovery. Walter Scott wrote to a friend : 

" The half hour between waking and rising has all my life 
proved propitious to any task which was exercising my invention. 
... It was always when I first opened my eyes that the desired 
ideas thronged upon me." 

Baker finds lying in the bath the ideal time and suggests that 
Archimedes hit upon his famous principle in the bath because of 
the favourable conditions and not because he noticed the 
buoyancy of his body in water. The favourable effects of the bed 



and the bath are probably due to complete freedom from dis- 
traction and to the fact that all the circumstances are conducive 
to reverie. Others attest to the value of leisure or of relaxing 
light occupations such as walking in the country or pottering in 
the garden. Hughlings Jackson used to advise his students to sit 
in a comfortable chair after the day's work was over and allow 
their thoughts to wander around things which had interested 
them during the day and write down the ideas that came. 

It is evident that to get bright ideas the scientist needs time 
for meditation. The favourable effect of temporary abandonment 
may be to escape from unprofitable conditioned thinking. Intense 
concentration on a problem too long continued may produce a 
state of mental blockade such as may occur when you try too 
hard to recall something that has slipped from your mind. 

According to Wallas^ ^ intuitions always appear at the fringe of 
consciousness, not at the focus. He considers that an effort should 
be made to grasp them and that a watch should be kept for 
valuable ideas in the eddies and backwashes rather than in the 
main current of thought. 

It is said that certain people get some kind of warning preced- 
ing an intuition. They become aware that something of that 
nature is imminent without knowing exactly what it will be. 
Wallas calls this " intimation ". This curious phenomenon does 
not seem to be at all general. 

My colleague, F. M. Burnet, finds that intuitions come to him 
mainly when he is writing and, unlike most people, rarely when 
he is relaxing. My own experience is that when I have been con- 
centrating on a subject for several days, it keeps coming back 
into my mind after I have stopped deliberately working on it. 
During a lecture, social evening, concert or cinema my thoughts 
will frequently revert to it and then sometimes after a few 
moments of conscious thought a new idea will occur. Occasionally 
the idea springs into the consciousness with Uttle or perhaps no 
preliminary conscious thinking. The brief preliminary conscious 
thinking may be similar to Wallas' "intimation", and can easily 
be missed or forgotten. A number of people have commented 
on the favourable influence of music but there is by no means 
universal agreement on this point. I find some, but not all, 
forms of music conducive to intuitions, both when I am attending 



an entertainment and when I am writing. The enjoyment of 
music is rather similar, emotionally, to the enjoyment derived 
from creative mental activity, and suitable music induces the right 
mood for productive thought. 

Elsewhere mention has been made of the tremendous emotional 
stimulus many people get when they either make a new discovery 
or get a brilliant intuition. Possibly this emotional reaction is 
related to the amount of emotional and mental effort that has 
been invested, as it were, in the problem. Also there is the sudden 
release from all the frustrations that have been associated with 
work on the problem. In this connection it is interesting to note 
the revealing statement of Claude Bernard : 

" Those who do not know the torment of the unknown cannot 
have the joy of discovery." 

Emotional sensitivity is perhaps a valuable attribute for a scien- 
tist to possess. In any event the great scientist must be regarded 
as a creative artist and it is quite false to think of the scientist 
as a man who merely follows rules of logic and experiment. 
Some of the masters of the art of research have displayed 
artistic talents in other directions. Einstein was a keen musician 
and so was Planck. Pasteur and Bernard early showed consfder- 
able promise in painting and play-writing, respectively. Nicolle 
comments on the interesting and curious fact that the ancient 
Peruvian language had a single word (hamavec) for both poet 
and inventor. ^^ 

Technique of seeking and capturing intuitions 

It may be useful to recapitulate and set out systematically the 
conditions which most people find conducive to intuition. 

(a) The most important prerequisite is prolonged contemplation 
of the problem and the data until the mind is saturated with it. 
There must be a great interest in it and desire for its solution. The 
mind must work consciously on the problem for days in order 
to get the subconscious mind working on it. Naturally the more 
relevant data the mind has to work on, the better are the chances 
of reaching a conclusion. 

(b) An important condition is freedom from other problems 
or interests competing for attention, especially worry over private 



Referring to these two prerequisites Piatt and Baker say : 

" No matter how diligently you apply your conscious thought 
to your work during office hours, if you are not really wrapped 
up in your work sufficiently to have your mind unconsciously 
revert to it at every opportunity, or if you have problems of so 
much more urgency that they crowd out the scientific problems, 
then you can expect little in the way of an intuition." 

(c) Another favourable condition is freedom from interruption 
or even fear of interruption or any diverting influence such as 
interesting conversation within earshot or sudden and excessively 
loud noises. 

(d) Most people find intuitions are more likely to come during 
a period of apparent idleness and temporary abandonment of the 
problem following periods of intensive work. Light occupations 
requiring no mental effort, such as walking in the country, 
bathing, shaving, travelhng to and from work, are said by some 
to be when intuitions most often appear, probably because under 
these circumstances there is freedom from distraction or interrup- 
tion and the conscious mind is not so occupied as to suppress 
anything interesting arising in the subconscious. Others find lying 
in bed most favourable and some people deliberately go over the 
problem before going to sleep and others before rising in the 
morning. Some find that music has a helpful influence but it is 
notable that only very few consider that they get any assistance 
from tobacco, coffee or alcohol. A hopeful attitude of mind 
may help. 

{e) Positive stimulus to mental activity is provided by some form 
of contact with other minds : (i) discussion with either a colleague 
or a lay person; (ii) writing a report on the investigation, or giving 
a talk on it ; (iii) reading scientific articles, including those giving 
views with which one disagrees. When reading articles on topics 
quite unrelated to the problem, the concept underlying a 
technique or principle may be absorbed and thrown out again as 
an intuition relating to one's own work. 

(/) Having considered the mental technicalities of deliberately 
seeking intuitions, there remains one further important practical 
point. It is a common experience that new ideas often vanish 
within a minute or so of their appearance if an effort is not made 
to capture them by focusing attention on them long enough to 



fix them in the memory. A valuable device which is widely used 
is to make a habit of carrying pencil and paper and noting down 
original ideas as they flash into the mind. It is said that Thomas 
Edison had a habit of jotting down almost every thought that 
occurred to him, however insignificant it may have appeared at 
the moment. This technique has also been much used by poets 
and musicians, and Leonardo da Vinci's notes provide a classical 
example of its use in the arts. Ideas coming during sleep are 
likely to be particularly elusive, and some psychologists and 
scientists always leave a pencil and paper nearby; this is also 
useful for capturing ideas which occur before one goes to sleep 
or while lying in bed in the morning. Ideas often make their 
appearance in the fringe of consciousness when one is reading, 
writing or otherwise engaged mentally on a theme which it is 
not desirable to interrupt. These ideas should be roughly jotted 
down as quickly as possible ; this not only preserves them but also 
serves the useful purpose of getting them "off your mind" with 
the minimum interruption to the main interest. Concentration 
requires that the mind should not be distracted by retaining ideas 
on the fringe of consciousness. 

(g) Three very important adverse influences have already been 
mentioned ; interruption, worry and competing interests. It takes 
time to get your mind "warmed up" and working efficiently on 
a subject, holding a mass of relevant data on the fringe of 
consciousness. Interruptions disturb this delicate complex and 
break the mood. Also mental and physical fatigue, too constant 
working on the problem (especially under pressure), petty irrita- 
tions and really distracting types of noise can miUtate against 
creative thinking. These remarks do not conflict with what is said 
in Chapter Eleven about the best work sometimes being done 
under adversity and mental stress. There I am referring rather 
to the deep-seated problems of life which sometimes may drive 
one to work in an attempt to escape them. In this chapter I am 
speaking of the immediate problems of everyday life. 

Scientific taste 

This seems the most appropriate place to discuss the concept 
"scientific taste". Hadamard and others have made the interesting 
observation that there is such a thing as scientific taste, just as 



there is a literary and an artistic taste/" Dale speaks of "the 
subconscious reasoning which we call instinctive judgment 'V'^ 
W. Ostwald*^ refers to "scientific instinct", and some people use 
the words "intuition" and "feeling" in this connection, by which 
they mean the same thing, but it seems to me more correct to 
call this faculty taste. It is probably synonymous with "personal 
judgment", which some scientists would probably prefer, but 
I think that expression is even less illuminating than is "taste". 
It is perhaps more exact to say that taste is that on which we 
base our personal judgment. 

Taste can perhaps best be described as a sense of beauty or 
aesthetic sensibility, and it may be reUable or not, depending on 
the individual. Anyone who has it simply feels in his mind that 
a particular line of work is of interest for its own sake and worth 
following, perhaps without knowing why. How reUable one's 
feelings are can be determined only by the results. The concept 
of scientific taste may be explained in another way by saying 
that the person who possesses the flair for choosing profitable lines 
of investigation is able to see further whither the work is leading 
than are other people, because he has the habit of using his 
imagination to look far ahead instead of restricting his thinking 
to established knowledge and the immediate problem. He may 
not be able to state explicitly his reasons or envisage any particular 
hypothesis, for he may see only vague hints that it leads towards 
one or another of several crucial questions. 

An illustration of taste in non-scientific matters is the choice 
of words and composition of sentences when writing. Only 
occasionally is it necessary to check the correctness of the language 
used by submitting it to grammatical analysis; usually we just 
"feel" that the sentence is correct or not. The elegance and 
aptness of the English which is produced largely automatically 
is a function of the taste we have acquired by training in 
choice and arrangement of words. In research, taste plays an 
important part in choosing profitable subjects for investigation, 
in recognising promising clues, in intuition, in deciding on a 
course of action where there are few facts with which to reason, 
in discarding hypotheses that require too many modifications and 
in forming an opinion on new discoveries before the evidence is 



Although, as with other tastes, people may be endowed with 
the capacity for scientific taste to varying degrees, it may also be 
cultivated by training oneself in the appreciation of science, as, 
for example, in reading about how discoveries have been made. 
As with other tastes, taste in science will only be found in people 
with a genuine love of science. Our taste derives from the 
summation of all that we have learnt from others, experienced 
and thought. 

Some scientists may have difficulty in comprehending such an 
abstract concept as taste, and some may find it unacceptable, 
because all the scientist's training is toward making him eliminate 
subjective influences from his work. No one would dispute the 
policy of keeping the subjective element out of experimentation, 
observation and technical procedures to the greatest possible 
extent. How far such a pohcy can effectively be carried out in a 
scientist's thinking is more open to question. Most people do not 
realise how often opinions that are supposed to be based on reason 
are in fact but rationalisations of prejudice or subjective motives. 
There is a very considerable part of scientific thinking where 
there is not enough sound knowledge to allow of effective 
reasoning and here the judgment will inevitably be largely 
influenced by taste. In research we continually have to take action 
on issues about which there is very little direct evidence. There- 
fore, rather than delude ourselves, I think it is wise to face the 
fact of subjective judgment and accept the concept of scientific 
taste, which seems a useful one. But by accepting the idea, I do 
not mean to suggest that we should adopt taste as a guide in 
cases where there is enough evidence on which to base an 
objectively reasoned judgment. The phrase, "scientific taste", 
must not be allowed to blind us to the risks which are associated 
with all subjective thinking. 


Intuition is used here to mean a clarifying idea that springs 
suddenly into the mind. It by no means always proves to be 

The conditions most conducive to intuitions are as follows : 
(a) The mind must first be prepared by prolonged conscious 
puzzling over the problem, (b) Competing interests or worries are 



inimical to intuitions, {c) Most people require freedom from 
interruptions and distractions, (d) Intuitions often make their 
appearance when the problem is not being worked on. (e) Positive 
stimuli are provided by intellectual contacts with other minds 
such as in discussion, critical reading or writing. (/) Intuitions 
often disappear from the mind irretrievably as quickly as they 
come, so should be written down, {g) Unfavourable influences 
include, in addition to interruptions, worry and competing 
interests, also mental or physical fatigue, too constant working 
on a problem, petty irritations and distracting types of noises. 
Often in research our thoughts and actions have to be guided 
by personal judgment based on scientific taste. 




" Discovery should come as an adventure rather than as 
the result of a logical process of thought. Sharp, prolonged 
thinking is necessary that we may keep on the chosen road, 
but it does not necessarily lead to discovery." 

— Theobald Smpth 

Limitations and hazards 

BEFORE considering the role of reason in research it may be 
useful to discuss the limitations of reason. These are more 
serious than most people realise, because our conception of science 
has been given us by teachers and authors who have presented 
science in logical arrangement and that is seldom the way in which 
knowledge is actually acquired. 

Everyday experience and history teach us that in the biological 
and medical sciences reason seldom can progress far from the 
facts without going astray. The scholasticism and authoritarianism 
prevailing during the Middle Ages was incompatible with science. 
With the Renaissance came a change in outlook : the beUef that 
things ought and must behave according to accepted views 
(mostly taken from the classics) was supplanted by a desire to 
observe things as they really are, and human knowledge began 
to grow again. Francis Bacon had a great influence on the 
development of science mainly, I think, because he showed that 
most discoveries had been made empirically rather than by use 
of deductive logic. In 1 605 he said : 

" Men are rather beholden . . . generally to chance, or anything 

else, than to logic, for the invention of arts and sciences ",* 

and in 1620, 

" the present system of logic rather assists in confirming and 
rendering inveterate the errors founded on vulgar notions, than 
in searching after truth, and is therefore more hurtful than 
useful." 7 



Later the French philosopher Rene Descartes made people realise 
that reason can land us in endless fallacies. His golden rule was : 

" Give unqualified assent to no propositions but those the 
truth of which is so clear and distinct that they cannot be 

Every child, indeed one might even say, every young verte- 
brate, discovers gravity; and yet modern science with all its 
knowledge cannot yet satisfactorily " explain " it. Not only are 
reason and logic therefore insufficient to provide a means of 
discovering gravity without empirical knowledge of it, but all 
the reason and logic apphed in classical times did not even 
enable inteUigent men to deduce correctly the elementary facts 
concerning it. 

F. C. S. Schiller, a modem philosopher, has made some illum- 
inating comments on the use of logic in science and I shall quote 
from him at length : 

" Among the obstacles to scientific progress a high place must 
certainly be assigned to the analysis of scientific procedure which 
logic has provided. ... It has not tried to describe the methods 
by which the sciences have actually advanced, and to extract . . . 
rules which might be used to regulate scientific progress, but has 
freely re-arranged the actual procedure in accordance with its 
prejudices, for the order of discovery there has been substituted 
an order of proof."®" 

Credence of the logician's view has been encouraged by the 
method generally adopted in the writing of scientific papers. 
The logical presentation of results which is usually followed is 
hardly ever a chronological or full account of how the investi- 
gation was actually carried out, for such would often be dull and 
difficult to follow and, for ordinary purposes, wasteful of space. 
In his book on the writing of scientific papers, Allbutt specifically 
advocates that the course of the research should not be followed 
but that a deductive presentation should be adopted. 

To quote again from Schiller, who takes an extreme view : 

" It is not too much to say that the more deference men of 
science have paid to logic, the worse it has been for the scientific 
value of their reasoning. . . . Fortunately for the world, however, 
the great men of science have usually been kept in salutary 
ignorance of the logical tradition." ®° 



He goes on to say that logic was developed to regulate debates in 
the Greek schools, assemblies and law-courts. It was necessary to 
determine which side won, and logic served this purpose, but it 
should not occasion surprise that it is quite unsuitable in science, 
for which it was never intended. Many logicians emphatically 
declare that logic, interested in correctness and validity, has 
nothing at all to do with productive thinking. 

Schiller goes even further in his criticism of traditional logic 
and says that not only is it of little value in making new dis- 
coveries, but that history has shown it to be of little value in 
recognising their validity or ensuring their acceptance when they 
have been proclaimed. Indeed, logical reasoning has often 
prevented the acceptance of new truths, as is illustrated by the 
persecution to which the great discoverers have so often been 

" The slowness and difficulty with which the human race makes 
discoveries and its blindness to the most obvious facts, if it 
happens to be unprepared or unwilling to see them, should suffice 
to show that there is something gravely wrong about the logician's 
account of discovery." 

Schiller was protesting mainly against the view of the scientific 
method expounded by certain logicians in the latter half of the 
nineteenth century. Most modem philosophers concerning them- 
selves with the scientific method do not interpret this phrase as 
including the art of discovery, which they consider to be outside 
their province. They are interested in the philosophical implica- 
tions of science. 

Wilfred Trotter^* also had some provocative things to say 
about the poor record which reason has in the advancement of 
scientific knowledge. Not only has it few discoveries to its credit 
compared to empiricism, he says, but often reason has obstructed 
the advance of science owing to false doctrines based on it. In 
medicine particularly, practices founded on reason alone have 
often prevailed for years or centuries before someone with an 
independent mind questioned them and in many cases showed 
they were more harmful than beneficial. 

Logicians distinguish between inductive reasoning (from par- 
ticular instances to general principles, from facts to theories) and 
deductive reasoning (from the general to the particular, applying 



a theory to a particular case). In induction one starts from 
observed data and develops a generalisation which explains the 
relationships between the objects observed. On the other hand, in 
deductive reasoning one starts from some general law and applies 
it to a particular instance. Thus in deductive reasoning the derived 
conclusion is contained within the original premiss, and should 
be true if the premiss is true. 

Since deduction consists of applying general principles to further 
instances, it cannot lead us to new generalisations and so cannot 
give rise to major advances in science. On the other hand the 
inductive process is at the same time less trustworthy but more 
productive. It is more productive because it is a means of arriving 
at new theories, but is less trustworthy because starting from a 
collection of facts we can often infer several possible theories, all 
of which cannot be true as some may be mutually incompatible ; 
indeed none of them may be true. 

In biology every phenomenon and circumstance is so complex 
and so poorly understood that premisses are not clear-cut and 
hence reasoning is unreliable. Nature is often too subtle for our 
reasoning. In mathematics, physics and chemistry the basic 
premisses are more firmly established and the attendant circum- 
stances can be more rigidly defined and controlled. Therefore 
reason plays a rather more dominant part in extending knowledge 
in these sciences. Nevertheless the mathematician Poincare said : 
" Logic has very Httle to do with discovery or invention." Similar 
views were expressed by Planck and Einstein (pp. 55, 57). The 
point here is that inductions are usually arrived at not by the 
mechanical application of logic but by intuition, and the course 
of our thoughts is constantly guided by our personal judgment. 
On the other hand the logician is not concerned with the way 
the mind functions but with logical formulation. 

From his experience in finding that his hypotheses always had 
to be abandoned or at least greatly modified Darwin learnt to 
distrust deductive reasoning in the biological sciences. He said : 

" I must begin with a good body of facts, and not from 
principle, in which I always suspect some fallacy."^* 

A basic difficulty in applying reason in research derives from 
the fact that terms often cannot be defined accurately and 



premisses are seldom precise or unconditionally true. Especially 
in biology premisses are only true under certain circumstances. 
For careful reasoning and clarity of thought one should first 
define the terms one uses but in biology exact definitions are often 
difficult or impossible to arrive at. Take, for example, the 
statement " influenza is caused by a virus." Influenza w^as 
originally a clinical concept, that is to say, a disease defined on 
clinical characters. We now know that diseases caused by several 
different microbes have been embraced by what the clinician 
regards as influenza. The virus worker would now prefer to 
define influenza as a disease caused by a virus with certain 
characters. But this only passes on the difficulty to the defining 
of an influenza virus which in turn escapes precise definition. 

These difficulties are to some extent resolved if we accept the 
principle that in all our reasoning we can deal only in probabili- 
ties. Indeed much of our reasoning in biology is more aptly 
termed speculation. 

I have mentioned some limitations inherent in the application 
of logical processes in science; another common source of error 
is incorrect reasoning, such as committing some logical fallacy. 
It is a delusion that the use of reason is easy and needs no training 
or special caution. In the following section I have tried to outline 
some general precautions which it may be helpful to keep in mind 
in using reason in research. 

Some safeguards in use of reason in research 

The first consideration is to examine the basis from which we 
start reasoning. This involves arriving at as clear an understanding 
as possible of what we mean by the terms we employ, and examin- 
ing our premisses. Some of the premisses may be well-established 
facts or laws, while others may be purely suppositions. It is often 
necessary to admit provisionally some assumptions that are not 
well established, in which case one needs to be careful not to 
forget that they are only suppositions. Michael Faraday warned 
against the tendency of the mind " to rest on an assumption " and 
when it appears to fit in with other knowledge to forget that it 
has not been proved. It is generally agreed that unverified 
assumptions should be kept down to the bare minimum and the 



hypothesis with the fewest assumptions is to be preferred. (This 
is known as the maxim of parsimony, or " Occam's Razor ". It 
was propounded by William of Occam in the fourteenth century.) 

How easy it is for unverified assumptions to creep into our 
reasoning unnoticed ! They are often introduced by expressions 
such as "obviously", "of course", "surely". I would have 
thought that it was a fairly safe assumption that well-fed animals 
live longer on the average that underfed ones, but in recent 
experiments mice whose diet was restricted to a point where their 
growth rate was below normal Uved much longer than mice 
allowed to eat as much as they wished. 

Having arrived at a clear understanding of the basis from 
which we start, at every step in our reasoning it is essential to 
pause and consider whether all conceivable alternatives have been 
taken into account. The degree of uncertainty or supposition is 
usually greatly magnified at each step. 

It is important not to confuse facts with their interpretations, 
-tbatJs to say, to distinguish between data and generalisations. 
Facts are particular observational data relating to the past or 
present. To take an obvious illustration : it may be a fact that 
when a certain drug was administered to rabbits it killed them, 
but to say that the drug is poisonous for rabbits is not a statement 
of a fact but a generalisation or law arrived at by induction. The 
change from the past tense to the present usually involves stepping 
from the facts to the induction. It is a step which must often be 
taken but only with an understanding of what one is doing. 
Confusion may also arise from the way in which the results are 
interpreted : strictly the facts arising from experiments can only 
be described by a precise statement of what occurred. Often in 
describing an experiment we interpret the results into other terms, 
perhaps without realising we are departing from a statement of 
the facts. 

A difficulty we are always up against is that we have to argue 
from past and present to the future. Science, to be of value, must 
predict. We have to reason from data obtained in the past by 
experiment and observation, and plan accordingly for the future. 
This presents special difficulties in biology because, owing to the 
incompleteness of our knowledge, we can seldom be sure that 
changed circumstances in the future may not influence the results. 



Take, for example, the testing of a new vaccine against a disease. 
The vaccine may prove effective in several experiments but we 
must still be cautious in saying it will be effective in future. 
Influenza vaccine gave a considerable degree of protection in large 
scale trials in U.S.A. in 1943 and 1945, but against the next 
epidemic in 1947 it was of no value. Regarded as a problem in 
logic the position is that by inductive inference from our data we 
arrive at a generalisation (for instance, that the vaccine is effec- 
tive). Then in future when we wish to guard against the disease we 
use this generalisation deductively and apply it to the particular 
practical problem of protecting certain people. The difficult 
point in the reasoning is, of course, making the induction. Logic 
has little to say here that is of help to us. All we can do is to 
refrain from generalising until we have collected fairly extensive 
data to provide a wide basis for the induction and regard as 
tentative any conclusion based on induction or, as we more often 
hear in everyday language, be cautious with generalisations. 
Statistics help us in drawing conclusions from our data by ensur- 
ing that our conclusions have a certain reliability, but even 
statistical conclusions are strictly valid only for events which have 
already occurred. 

Generalisations can never be proved. They can be tested by 
seeing whether deductions made from them are in accord with 
experimental and observational facts, and if the results are not 
as predicted, the hypothesis or generalisation may be disproved. 
But a favourable result does not prove the generalisation, because 
the deduction made from it may be true without its being true. 
Deductions, themselves correct, may be made from palpably 
absurd generalisations. For instance, the truth of the hypothesis 
that plague is due to evil spirits is not established by the correct- 
ness of the deduction that you can avoid the disease by keeping 
out of the reach of the evil spirits. In strict logic a generalisation 
is never proved and remains on probation indefinitely, but if it 
survives all attempts at disproof it is accepted in practice, 
especially if it fits well into a wider theoretical scheme. 

If scientific logic shows we must be cautious in arriving at 
generalisations ourselves, it shows for the same reasons that we 
should not place excessive trust in any generalisation, even widely 
accepted theories or laws. Newton did not regard the laws he 



formulated as the ultimate truth, but probably most following 
him did until Einstein showed how well-founded Newton's 
caution had been. In less fundamental matters how often do we 
see widely accepted notions superseded ! 

Therefore the scientist cannot afford to allow his mind to 
become fixed, with reference not only to his own opinions but 
also to prevailing ideas. Theobald Smith said : 

" Research is fundamentally a state of mind involving con- 
tinual re-examination of doctrines and axioms upon which 
current thought and action are based. It is, therefore, critical of 
existing practices."*^ 

No accepted idea or " established principle " should be regarded 
as beyond being questioned if there is an observation challenging 
it. Bernard wrote : 

" If an idea presents itself to us, we must not reject it simply 
because it does not agree with the logical deductions of a reign- 
ing theory." 

Great discoveries have been made by means of experiments 
devised with complete disregard for well accepted beliefs. 
Evidently it was Darwin who introduced the expression " fool's 
experiment " to refer to such experiments, which he often under- 
took to test what most people would consider not worth testing. 

People in most other walks of Ufe can allow themselves the 
indulgence of fixed ideas and prejudices which make thinking 
so much easier, and for all of us it is a practical necessity to hold 
definite opinions on many issues in everyday life, but the research 
worker must try to keep his mind malleable and avoid holding 
set ideas in science. We have to strive to keep our mind receptive 
and to examine suggestions made by others fairly and on their 
own merits, seeking arguments for as well as against them. We 
must be critical, certainly, but beware lest ideas be rejected 
because an automatic reaction causes us to see only the arguments 
against them. We tend especially to resist ideas competing with 
our ov^m. 

A useful habit for scientists to develop is that of not trusting 
ideas based on reason only. As Trotter says, they come into the 
mind often with a disarming air of obviousness and certainty. 
Some consider that there is no such thing as pure reasoning, that 
is to say, except where mathematical symbols are involved. 



Practically all reasoning is influenced by feelings, prejudice and 
past experience, albeit often subconsciously. Trotter wrote : 

" The dispassionate intellect, the open mind, the unprejudiced 
observer, exist in an exact sense only in a sort of intellectualist 
folk-lore; states even approaching them cannot be reached with- 
out a moral and emotional effort most of us cannot or will not 

A trick of the mind well known to psychologists is to " rational- 
ise ", that is, to justify by reasoned ai^ument a view which in 
reality is determined by preconceived judgment in the sub- 
conscious mind, the latter being governed by self-interest, 
emotional considerations, instinct, prejudice and similar factors 
which the person usually does not realise or admit even to him- 
self In somewhat similar vein is W. H. George's warning against 
believing that things in nature ought to conform to certain 
patterns or standards and regarding all exceptions as abnormal. 
He says that the " should-ought mechanism " has no place what- 
ever in research, and its complete abandonment is one of the 
foundation stones of science. It is premature, he considers, to 
worry about the technique of experimentation until a man has 
become dissatisfied with the " should-ought " way of thinking. 

It has been said by some that scientists should train them- 
selves to adopt a disinterested attitude to their work. I cannot 
agree with this view and think the investigator should try to 
exercise sufficient self-control to consider fairly the evidence 
against a certain outcome for which he fervently hopes, rather 
than to try to be disinterested. It is better to recognise and face 
the danger that our reasoning may be influenced by our wishes. 
Also it is unwise to deny ourselves the pleasure of associating 
ourselves whole-heartedly with our ideas, for to do so would be 
to undermine one of the chief incentives in science. 

It is important to distinguish between interpolation and extra- 
polation. Interpolating means filling in a gap between estabUshed 
facts which form a series. When one draws a curve on a graph by 
connecting the points one interpolates. Extrapolating is going 
beyond a series of observations on the assumption that the same 
trend continues. Interpolation is considered permissible for most 
purposes provided one has a good series of data to work from, 
but extrapolation is much more hazardous. Apparently obvious 



extensions of our theories beyond the field in which they have 
been tested often lead us astray. The process of extrapolation is 
rather similar to implication and is useful in providing suggestions. 

A useful aid in getting a clear understanding of a problem is 
to write a report on all the information available. This is helpful 
when one is starting on an investigation, when up against a 
difficulty, or when the investigation is nearing completion. Also 
at the beginning of an investigation it is useful to set out clearly 
the questions for which an answer is being sought. Stating the 
problem precisely sometimes takes one a long way toward the 
solution. The systematic arrangement of the data often discloses 
flaws in the reasoning, or alternative lines of thought which had 
been missed. Assumptions and conclusions at first accepted as 
" obvious " may even prove indefensible when set down clearly 
and examined critically. Some institutions make it a rule for all 
research workers to furnish a report quarterly on the work done, 
and work planned. This is useful not only for the director to keep 
in touch with developments but also to the workers themselves. 
Certain directors prefer verbal reports which they consider more 
useful in helping the research worker " get his ideas straight ". 

Careful and correct use of language is a powerful aid to 
straight thinking, for putting into words precisely what we 
mean necessitates getting our own minds quite clear on what 
we mean. It is with words that we do our reasoning, and 
writing is the expression of our thinking. Discipline and training 
in writing is probably the best training there is in reasoning. 
Allbutt has said that slovenly writing reflects slovenly thinking, 
and obscure writing usually confused thinking. The main aim in 
scientific reports is to be as clear and precise as possible and make 
each sentence mean exactly what it is intended to and be incap- 
able of other interpretation. Words or phrases that do not have 
an exact meaning are to be avoided because once one has given 
a name to something, one immediately has a feeling that the 
position has been clarified, whereas often the contrary is true. 
"A verbal cloak of ignorance is a garment that often hinders 
progress." ^^ 

The role of reason in research 

Although discoveries originate more often from unexpected 
experimental results or observations, or from intuitions, than 



directly from logical thought, reason is the principle agent in most 
other aspects of research and the guide to most of our actions. 
It is the main tool in formulating hypotheses, in judging the 
correctness of ideas conjured up by imagination and intuition, 
in planning experiments and deciding what observations to 
make, in assessing the evidence and interpreting new facts, in 
making generalisations and finally in finding extensions and 
applications of a discovery. 

The methods and functions of discovery and proof in research 
are as different as are those of a detective and of a judge in a 
court of law. While playing the part of the detective the investi- 
gator follows clues, but having captured his alleged fact, he turns 
judge and examines the case by means of logically arranged 
evidence. Both functions are equally essential but they are 

It is in " factual " discoveries in biology that observation and 
chance — empiricism — plays such an important part. But facts 
obtained by observation or experiment usually only gain signi- 
ficance when we use reason to build them into the general body 
of knowledge. Darwin said : 

" Science consists in grouping facts so that general laws or 
conclusions may be drawn from them."^* 

In research it is not sufficient to collect facts; by interpreting 
them, by seeing their significance and consequences we can often 
go much further. Walshe considers that just as important as 
making discoveries is what we make of our discoveries, or for 
that matter, of those of other people. ^°° To help retain and use 
information our minds require a rationalised, logically consistent 
body of knowledge. Hughlings Jackson said that 

" We have multitudes of facts, but we require, as they accumu- 
late, organisations of them into higher knowledge; we require 
generalisations and working hypotheses." 

The recognition of a new general principle is the consummation 
of scientific study. 

Discoveries originating from so-called chance observations, 
from unexpected results in experiments or from intuitions are 
dramatic and arrest attention more than progress resulting from 
purely rational experimentation in which each step follows 



logically on the previous one so that the discovery only gradually 
unfolds. Therefore the latter, less spectacular process may be 
responsible for more advances than has been imphed in the other 
chapters of this book. Moreover, as Zinsser said : 

" The preparatory accumulation of minor discoveries and of 
accurately observed details ... is almost as important for the 
mobilisation of great forward drives as the periodic correlation 
of these disconnected observations into principles and laws by 
the vision of genius."^"* 

Often when one looks into the origin of a discovery one finds 
that it was a much more gradual process than one had imagined. 

In nutritional research, the discovery of the existence of the 
various vitamins was in a number of instances empirical, but sub- 
sequent development of knowledge of them was rational. Usually 
in chemotherapy, after the initial empirical discovery opening up 
the field, rational experimentation has led to a series of improve- 
ments, as in the development of sulphathiazole, sulphamerazine, 
sulphaguanidine, etc., following on the discovery of the thera- 
peutic value of sulphanilamide, the first compound of this type 
found to have bacteriostatic properties. 

As described in the Appendix, Fleming followed up a chance 
observation to discover that the mould Penicillium notatum 
produced a substance that had bacteriostatic properties and was 
non-toxic. However, he did not pursue it sufficiently to develop 
a chemotherapeutic agent and the investigation was dropped. 
During the latter quarter of the last century and first part of this 
there were literally dozens of reports of discoveries of antibacterial 
substances produced by bacteria and fungi.^^ Even penicillin 
itself was discovered before Fleming or Rorey."^ Quite a number 
of writers had not only suggested that these products might be use- 
ful therapeutically but had employed them and in some instances 
good results seem to have been obtained.^^ But all these empirical 
discoveries were of little consequence until Florey, by a deliber- 
ately planned, systematic attack on the problem, produced peni- 
cillin in a relatively pure and stable form and so was able to 
demonstrate its great clinical value. Often the original discovery, 
like the crude ore from the mine, is of little value until it has 
been refined and fully developed. This latter process, less specta- 
cular and largely rational, usually requires a diflferent type of 



scientist and often a team. The role of reason in research is not 
so much in exploring the frontiers of knowledge as in developing 
the findings of the explorers. 

A type of reasoning not yet mentioned is reasoning by analogy, 
which plays an important part in scientific thought. An analogy 
is a resemblance between the relationship of things, rather than 
between the things themselves. When one perceives that the 
relationship between A and B resembles the relationship between 
X and T on one point, and one knows that A is related to 5 in 
various other ways, this suggests looking for similar relationships 
between X and T. Analogy is very valuable in suggesting clues or 
hypotheses and in helping us comprehend phenomena and 
occurrences we cannot see. It is continually used in scientific 
thought and language but it is as well to keep in mind that analogy 
can often be quite misleading and of course can never prove any- 

Perhaps it is relevant to mention here that modem scientific 
philosophers try to avoid the notion of cause and effect. The 
current attitude is that scientific theories aim at describing associa- 
tions between events without attempting to explain the relation- 
ship as being causal. The idea of cause, as implying an inherent 
necessity, raises philosophical difficulties and in theoretical physics 
the idea can be abandoned with advantage as there is then no 
longer the need to postulate a connection between the cause and 
effect. Thus, in this view, science confines itself to description — 
"how", not "why". 

This outlook has been developed especially in relation to 
theoretical physics. In biology the concept of cause and effect is 
still used in practice, but when we speak of the cause of an event 
we are really over-simplifying a complex situation. Very many 
factors are involved in bringing about an event but in practice we 
commonly ignore or take for granted those that are always present 
or well-known and single out as the cause one factor which is 
unusual or which attracts our attention for a special reason. The 
cause of an outbreak of plague may be regarded by the bacterio- 
logist as the microbe he finds in the blood of the victims, by the 
entomologist as the microbe-carrying fleas that spread the disease, 
by the epidemiologist as the rats that escaped from the ship and 
brought the infection into the port. 




The origin of discoveries is beyond the reach of reason. The 
role of reason in research is not hitting on discoveries — either 
factual or theoretical — but verifying, interpreting and developing 
them and building a general theoretical scheme. Most biological 
" facts " and theories are only true under certain conditions and 
our knowledge is so incomplete that at best we can only reason on 
probabilities and possibiUties. 




" Knowledge comes from noticing resemblances and 
recurrences in the events that happen around us." 

— Wilfred Trotter 


PASTEUR was curious to know how anthrax persists endemi- 
cally, recurring in the same fields, sometimes at intervals 
of several years. He was able to isolate the organisms from soil 
around the graves in which sheep dead of the disease had been 
buried as long as 1 2 years before. He was puzzled as to how the 
organism could resist sunlight and other adverse influences so 
long. One day while walking in the fields he noticed a patch of 
soil of different colour from the rest and asked the farmer the 
reason. He was told that sheep dead of anthrax had been buried 
there the previous year. 

" Pasteur, who always examined things closely, noticed on the 
surface of the soil a large number of worm castings. The idea 
then came to him that in their repeated travelling from the 
depth to the surface, the worms carried to the surface the earth 
rich in humus around the carcase, and with it the anthrax spores 
it contained. Pasteur never stopped at ideas but passed straight 
to the experiment. This justified his forecast. Earth contained 
in a worm, inoculated into a guinea-pig produced anthrax."^* 

This is a fine example of the value of direct personal observation. 
Had Pasteur done his thinking in an armchair it is unlikely that 
he would have cleared up this interesting bit of epidemiology. 

When some rabbits from the market were brought into Claude 
Bernard's laboratory one day, he noticed that the urine which 
they passed on the table was clear and acid instead of turbid and 
alkaline as is usual with herbivorous animals. Bernard reasoned 
that perhaps they were in the nutritional condition of carnivora 
from having fasted and drawn on their own tissues for susten- 



ance. This he confirmed by ahemately feeding and starving 
them, a process which he found altered the reaction of their 
urine as he had anticipated. This was a nice observation and 
would have satisfied most investigators, but not Bernard. He 
required a " counterproof ", and so fed rabbits on meat. This 
resulted in an acid urine as expected, and to complete the experi- 
ment he carried out an autopsy on the rabbits. To use his words : 

" I happened to notice that the white and milky lymphatics 
were first visible in the small intestine at the lower part of the 
duodenum, about 30 cm. below the pylorus. The fact caught 
my attention because in dogs they are first visible much higher 
in the duodenum just below the pylorus." 

On observing more closely, he saw that the opening of the 
pancreatic duct coincided with the position where the lymphatics 
began to contain chyle made white by emulsion of the fatty 
materials. This led to the discovery of the part played by pan- 
creatic juice in the digestion of fats.^^ 

Darwin relates an incident illustrating how he and a colleague 
failed to observe certain unexpected phenomena when they were 
exploring a valley : 

" Neither of us saw a trace of the wonderful glacial phenomena 
all around us; we did not notice plainly scored rocks, the 
perched boulders, the lateral and terminal moraines."' 


These things were not observed because they were not expected 
or specifically looked for. 

While watching the movements of the bacteria which cause 
butyric acid fermentation, Louis Pasteur noticed that when the 
organisms came near the edge of the drop they stopped moving. 
He guessed this was due to the presence of oxygen in the fluid 
near the air. Puzzling over the significance of this observation he 
concluded that there was no free oxygen where the bacteria were 
actively moving. From this he made the far reaching deduction 
that Ufe can exist without oxygen, which at that time was thought 
not possible. Further he postulated that fermentation is a meta- 
bolic process by which microbes obtain oxygen from organic sub- 
stances. These important i^leas which Pasteur later substantiated 
had their origin in the observation of a detail that many would 
not have noticed. 



Many of the anecdotes cited in Chapters Three and Four and 
in the Appendix also provide illustrations of the role of observa- 
tion in research. 

Some general principles in observation 

In discussing the thoroughly unreliable nature of eye-witness 
observation of everyday events, W. H. George says : 

" What is observed depends on who is looking. To get some 
agreement between observers they must be paying attention, 
their lives must not be consciously in danger, their prime neces- 
sities of life must preferably be satisfied and they must not be 
taken by surprise. If they are observing a transient phenomenon, 
it must be repeated many times and preferably they must not 
only look at, but must look for, each detail."*^ 

As an illustration of the difficulty of making careful observa- 
tions, he tells the following story. 

At a congress on psychology at Gottingen, during one of the 
meetings, a man suddenly rushed into the room chased by another 
with a revolver. After a scuffle in the middle of the room a shot 
was fired and both men rushed out again about twenty seconds 
after having entered. Immediately the chairman asked those 
present to write down an account of what they had seen. 
Although the observers did not know it at the time, the incident 
had been previously arranged, rehearsed and photographed. Of 
the forty reports presented, only one had less than 20 per cent 
mistakes about the principal facts, 14 had from 20 to 40 per cent 
mistakes, and 25 had more than 40 per cent mistakes. The most 
noteworthy feature was that in over half the accounts, 10 per 
cent or more of the details were pure inventions. This poor 
record was obtained in spite of favourable circumstances, for 
the whole incident was short and sufficiently striking to arrest 
attention, the details were immediately written down by people 
accustomed to scientific observation and no one was himself 
involved. Experiments of this nature are commonly conducted 
by psychologists and nearly always produce results of a similar 


Perhaps the first thing to realise about observations is that not 
only do observers frequently miss seemingly obvious things, but 
what is even more important, thev often invent quite false 



observations. False observations may be due to illusions, where 
the senses give wrong information to the mind, or the errors may 
have their origin in the mind. 

Illustrations of optical illusions can be provided from various 
geometrical figures (see, for example, George*^) and by distor- 
tions caused by the refraction of light when it passes through 
water, glass or heated air. Remarkable demonstrations of the 
unreliability of visual observations are provided by the tricks 
of " magicians " and conjurors. Another illustration of false 
information arising from the sense organs is provided by placing 
one hand in hot water and one in cold for a few moments and 
then plunging them both into tepid water. A curious fallacy of 
this nature was recorded by the ancient Greek historian, 
Herodotus : 

" The water of this stream is lukewarm at early dawn. At the 
time when the market fills it is much cooler; by noon it has 
grown quite cold; at this time therefore they water their gardens. 
As the afternoon advances, the coldness goes off, till, about 
sunset the water is once more lukewarm." 

In all probability the temperature of the water remained constant 
and the change noticed was due to the difference between water 
and atmospheric temperatures as the latter changed. Fallacious 
observations of a similar type can be shown to arise from illu- 
sions associated with sound. 

The second class of error in registering and reporting observa- 
tion has its origin in the mind itself Many of these errors can 
be attributed to the fact that the mind has a trick of unconsciously 
filling in gaps according to past experience, knowledge and con- 
scious expectations. Goethe has said : 

" We see only what we know." 

" We are prone to see what lies behind our eyes rather than what 
appears before them," an old saying goes. An illustration of this 
is seen in the cinema film depicting a lion chasing a negro. The 
camera shows now the lion pursuing, now the man fleeing, and 
after several repetitions of this we finally see the lion leap on 
something in the long grass. Even though the lion and the man 
may have at no time appeared on the screen together, most 
people in the audience are convinced they actually saw the lion 



leap on the man, and there have been serious protests that natives 
were sacrificed to make such a film. Another illustration of the 
subjective error is provided by the following anecdote. A 
Manchester physician, while teaching a ward class of students, 
took a sample of diabetic urine and dipped a finger in it to taste 
it. He then asked all the students to repeat his action. This they 
reluctantly did, making grimaces, but agreeing that it tasted 
sweet. " I did this," said the physician with a smile, " to teach 
you the importance of observing detail. If you had watched me 
carefully you would have noticed that I put my first finger in 
the urine but licked my second finger !" 

It is common knowledge that different people viewing the 
same scene will notice different things according to where their 
interests lie. In a country scene a botanist will notice the 
different species of plants, a zoologist the animals, a geologist 
the geological structures, a farmer the crops, farm animals, 
etc. A city dweller with none of these interests may see only 
a pleasant scene. Most men can pass a day in the company of 
a woman and afterwards have only the vaguest ideas about what 
clothes she wore, but most women after meeting another woman 
for only a few minutes could describe every article the other was 

It is quite possible to see something repeatedly without register- 
ing it mentally. For example, a stranger on arrival in London 
commented to a Londoner on the eyes that are painted on the 
front of many buses. The Londoner was surprised, as he had 
never noticed them. But after his attention had been called to 
them, during the next few weeks he was conscious of these eyes 
nearly every time he saw a bus. 

Changes in a familiar scene are often noticed even though the 
observer may not have been consciously aware of the details of 
the scene previously. Indeed sometimes an observer may be 
aware that something has changed in a familiar scene without 
being able to tell what the change is. Discussing this point, 
W. H. George says : 

" It seems as if the memory preserves something like a photo- 
graphic negative of a very familiar scene. At the next examina- 
tion this memory image is unconsciously placed over the visual 
image present, and, just as with two similar photographic nega- 












tives, attention is immediately attracted to the places where the 
two do not exactly fit, that is, where there is a change in one 
relative to the other. It is noteworthy that this remembered whole 
cannot always be recalled to memory so as to enable details to 
be described."*^ 

This analogy should not be taken too literally because the same 
phenomenon is seen with memory of other things such as 
stories or music. A child who is familiar with a story will often 
call attention to slight variations when it is retold even though he 
does not know it by heart himself George continues : 

" The perception of change seems to be a property of all of 
the sense organs, for changes of sound, taste, smell and tempera- 
ture are readily noticed. ... It might almost be said that a con- 
tinuous sound is only ' heard ' when it stops or the sound 
changes." ^^ 

If we consider that the comparison of the old and new images 
takes place in the subconscious, we can draw an analogy with 
the hypothesis as to how intuitions gain access to the conscious 
mind. One would expect the person to become aware of the 
notable facts, that is, the changes, even though he may be unable 
to bring all the details into consciousness. 

It is important to realise that observation is much more than 
merely seeing something; it also involves a mental process. In 
all observations there are two elements : {a) the sense-perceptual 
element (usually visual) and {b) the mental, which, as we have 
seen, may be partly conscious and partly unconscious. Where 
the sense-perceptual element is relatively unimportant, it is often 
difficult to distinguish between an observation and an ordinary 
intuition. For example, this sort of thing is usually referred to as 
an observation : "I have noticed that I get hay fever whenever 
I go near horses." The hay fever and the horses are perfectly 
obvious, it is the connection between the two that may require 
astuteness to notice at first, and this is a mental process not dis- 
tinguishable from an intuition. Sometimes it is possible to draw 
a line between the noticing and the intuition, e.g. Aristotle com- 
mented that on observing that the bright side of the moon is al- 
ways toward the sun, it may suddenly occur to the observer that 
the explanation is that the moon shines by the light of the sun. 



Similarly in three of the anecdotes given at the beginning of 
this chapter, the observation was followed by an intuition. 

Scientific observation 

We have seen how unreliable an observer's report of a complex 
situation often is. Indeed, it is very difficult to observe and 
describe accurately even simple phenomena. Scientific experi- 
ments isolate certain events which are observed by the aid of 
appropriate techniques and instruments which have been 
developed because they are relatively free from error and have 
been found to give reproducible results which are in accord 
with the general body of scientific knowledge. Claude Bernard 
distinguished two types of observation : (a) spontaneous or 
passive observations which are unexpected; and (b) induced or 
active observations which are deliberately sought, usually on 
account of an hypothesis. It is the former in which we are 
chiefly interested here. 

Eflfective spontaneous observation involves firstly noticing 
some object or event. The thing noticed will only become 
significant if the mind of the observer either consciously or 
unconsciously relates it to some relevant knowledge or past 
experience, or if in pondering on it subsequently he arrives at 
some hypothesis. In the last section attention was called to the 
fact that the mind is particularly sensitive to changes or differ- 
ences. This is of use in scientific observation, but what is more 
important and more difficult is to observe (in this instance mainly 
a mental process) resemblances or correlations between things 
that on the surface appeared quite unrelated. The quotation 
from Trotter at the beginning of this chapter refers to this 
point. It required the genius of Benjamin Franklin to see the 
relationship between frictional electricity and lightning. Recently 
veterinarians have recognised a disease of dogs which is manifest 
by encephalitis and hardening of the foot pads. Many cases of 
the disease have probably been seen in the past without anyone 
having noticed the surprising association of the encephalitis with 
the hard pads. 

One cannot observe everything closely, therefore one must 
discriminate and try to select the significant. When practising 
a branch of science, the " trained " observer deUberately looks 



for specific things which his training has taught him are 
significant, but in research he often has to rely on his own 
discrimination, guided only by his general scientific knowledge, 
judgment and perhaps an hypothesis which he entertains. As 
Alan Gregg, the Director of Medical Sciences for the Rockefeller 
Foundation has said : 

" Most of the knowledge and much of the genius of the 
research worker lie behind his selection of what is worth observ- 
ing. It is a crucial choice, often determining the success or failure 
of months of work, often differentiating the brilliant discoverer 
from the . . . plodder."*^ 

When Faraday was asked to watch an experiment, it is said 
that he would always 2isk what it was he had to look for but 
that he was still able to watch for other things. He was following 
the principle enunciated in the quotation from George in the 
preceding section, that preferably each detail should be looked 
for. However, this is of little help in making original observa- 
tions. Claude Bernard considered that one should observe an 
experiment with an open mind for fear that if we look only 
for one feature expected in view of a preconceived idea, we will 
miss other things. This, he said, is one of the greatest stumbling 
blocks of the experimental method, because, by failing to note 
what has not been foreseen, a misleading observation may be 
made. " Put off your imagination," he said, " as you take off 
your overcoat when you enter the laboratory." Writing of 
Charles Darwin, his son tells us that : 

" He wished to learn as much as possible from an experiment 
so he did not confine himself to observing the single point 
to which the experiment was directed, and his power of seeing 
a number of things was wonderful. . . . There was one quality of 
mind which seemed to be of special and extreme advantage in 
leading him to make discoveries. It was the power of never letting 
exceptions pass unnoticed."^' 

If, when we are experimenting, we confine our attention to 
only those things we expect to see, we shall probably miss the 
unexpected occurrences and these, even though they may at 
first be disturbing and troublesome, are the most likely to point 
the way to important unsuspected facts. It has been said that 
it is the exceptional phenomenon which is likely to lead to the 



explanation of the usual. When an irregularity is noticed, look 
for something with which it might be associated. In order to 
make original observations the best attitude is not to concentrate 
exclusively on the main point but to try and keep a look-out 
for the unexpected, remembering that observation is not passively 
watching but is an active mental process. 

Scientific observation of objects calls for the closest possible 
scrutiny, if necessary with the aid of a lens. The making of 
detailed notes and drawings is a valuable means of prompting 
one to observe accurately. This is the main reason for 
making students do drawings in practical classes. Sir MacFarlane 
Burnet has autopsied tens of thousands of mice in the course 
of his researches on influenza, but he examines the lungs of 
every mouse with a lens and makes a careful drawing of the 
lesions. In recording scientific observations one should always 
be as precise as possible. 

Powers of observation can be developed by cultivating the 
habit of watching things with an active, enquiring mind. It is 
no exaggeration to say that well developed habits of observation 
are more important in research than large accumulations of 
academic learning. The faculty of observation soon atrophies 
in modem civilisation, whereas with the savage hunter it may 
be strongly developed. The scientist needs consciously to develop 
it, and practical work in the laboratory and the clinic should assist 
in this direction. For example, when observing an animal, one 
should look over it systematically and consciously note, for in- 
stance, breed, age, sex, colour markings, points of conformation, 
eyes, natural orifices, whether the abdomen is full or empty, the 
mammary glands, condition of the coat, its demeanour and 
movements, any peculiarities and note its surroundings including 
any faeces or traces of food. This is, of course, apart from, or 
preliminary to, a clinical examination if the animal is ill. 

In carrying out any observation you look deliberately for 
each characteristic you know may be there, for any unusual 
feature, and especially for any suggestive associations or relation- 
ships among the things you see, or between them and what 
you know. By this last point I mean such things as noticing 
that on a plate culture some bacterial colonies inhibit or favour 
others in their vicinity, or in field observations any association 



between disease and type of pasture, weather or system of 
management. Most of the relationships observed are due to 
chance and have no significance, but occasionally one will lead 
to a fruitful idea. It is as well to forget statistics when doing 
this and consider the possibiUty of some significance behind 
slender associations in the observed data, even though they 
would be dismissed at a glance if regarded on a mathematical 
basis. More discoveries have arisen from intense observation 
of very limited material than from statistics appUed to large 
groups. The value of the latter Hes mainly in testing hypotheses 
arising from the former. While observing one should cultivate 
a speculative, contemplative attitude of mind and search for clues 
to be followed up. 

Training in observation follows the same principles as training 
in any activity. At first one must do things consciously and 
laboriously, but with practice the activities gradually become 
automatic and unconscious and a habit is established. Effective 
scientific observation also requires a good background, for only 
by being familiar with the usual can we notice something as 
being unusual or unexplained. 


Accurate observation of complex situations is extremely 
difficult, and observers usually make many errors of which 
they are not conscious. Effective observation involves noticing 
something and giving it significance by relating it to something 
else noticed or already known; thus it contains both an element 
of sense-perception and a mental element. 

It is impossible to observe everything, and so the observer 
has to give most of his attention to a selected field, but he 
should at the same time try to watch out for other things, 
especially anything odd. 




" Error is all around us and creeps in at the least oppor- 
tunity. Every method is imperfect." — Charles Nicolle. 

Mental resistance to new ideas 

WHEN the great discoveries of science were made they 
appeared in a very different light than they do now. 
Previous ignorance on the subject was rarely recognised, for 
either a blind eye was turned to the problem and people were 
scarcely aware of its existence, or there were weU accepted 
notions on the subject, and these had to be ousted to make way 
for the new conceptions. Professor H. Butterfield points out 
that the most difficult mental act of all is to re-arrange a familiar 
bundle of data, to look at it differently and escape from the 
prevailing doctrine.^" This was the great intellectual hurdle 
that confronted such pioneers as Galileo, but in a minor form 
it crops up with every important original discovery. Things 
that are now quite easy for children to grasp, such as the 
elementary facts of the planetary system, required the colossal 
intellectual feat of a genius to conceive when his mind was 
already conditioned with AristoteHan notions. 

WiUiam Harvey's discovery of the circulation of the blood 
might have been relatively easy but for the prevailing beliefs 
that the blood ebbed and flowed in the vessels, that there were 
two sorts of blood and that the blood was able to pass from 
one side of the heart to the other. His first cause for dissatisfac- 
tion with these doctrines was his finding of the direction in 
which the valves faced in the veins of the head and neck — a 
small stubborn fact which the current hypothesis did not fit. He 
dissected no fewer than eighty species of animals including rep- 
tiles, crustaceans and insects, and spent many years on the investi- 
gation. The big difficulty in establishing the conception of the 
circulation was the absence of any visible connection between 



the terminal arteries and the veins, and he had to postulate 
the existence of the capillaries, which were not discovered until 
later. Harvey could not demonstrate the circulation, so had to 
leave it as an inference. He required courage to announce how 
much blood he calculated that the heart pumped out. Harvey 
himself wrote : 

" But what remains to be said about the quantity and source 
of the blood which thus passes, is of so novel and unheard-of 
character that I not only fear injury to myself from the envy of 
a few, but I tremble lest I have mankind at large for my enemies, 
so much doth want and custom, that become as another nature, 
and doctrine once sown and that hath struck deep root, and 
respect for antiquity, influence all men : still the die is cast, and 
my trust is in my love of truth, and the candour that inheres in 
cultivated minds." ^"^ 

His fears were well founded for he was subjected to derision 
and abuse and his practice suffered badly. Only after a struggle 
of over twenty years did the circulation of the blood become 
generally accepted. 

Other illustrations of resistance to new ideas are provided by 
the stories about Jenner and Mules already recounted and that 
about Semmelweis given later in this chapter. 

Vesalius in his early anatomical studies related that he could 
hardly believe his own eyes when he found structures not in 
accord with Galen's descriptions. Lesser men did, in fact, 
disbelieve their own eyes, or at least thought that the subject 
for dissection or their own handiwork was at fault. It is often 
curiously difficult to recognise a new, unexpected fact, even 
when obvious. Only people who have never found themselves 
face to face with a new fact laugh at the inabihty of medieval 
observers to beUeve their own eyes. Teachers well know that 
students often ignore the results of their experiments and mistrust 
their observations if they do not coincide with their expecta- 

In nearly all matters the human mind has a strong tendency 
to judge in the light of its own experience, knowledge and 
prejudices rather than on the evidence presented. Thus new 
ideas are judged in the light of prevailing beHefs. If the ideas 
are too revolutionary, that is to say, if they depart too far from 



reigning theories and cannot be fitted into the current body of 
knowledge, they will not be acceptable. When discoveries are 
made before their time they are almost certain to be ignored 
or meet with opposition which is too strong to be overcome, 
so in most instances they may as well not have been made. 
Dr. Marjory Stephenson likens discoveries made in advance of 
their time to long salients in warfare by which a position may 
be captured. If, however, the main army is too far behind to 
give necessary support, the advance post is lost and has to be 
re-taken at a later date.*' 

McMunn discovered cytochrome in 1886, but it meant little 
and was ignored until Keilin rediscovered it thirty-eight years 
later and was able to interpret it. Mendel's discovery of the 
basic principles of genetics is another good example of inability 
of even the scientific world always to recognise the importance 
of a discovery. His work established the foundation of a new 
science, yet it was ignored for thirty-five years after it had been 
read to a scientific .society and published. Fisher has said that each 
generation seems to have found in Mendel's paper only what it 
expected to find and ignored what did not conform to its own 
expectations.^' His contemporaries saw only a repetition of 
hybridisation experiments already published, the next generation 
appreciated the importance of his views on inheritance but 
considered them difficult to reconcile with evolution. And now 
Fisher tells us that some of Mendel's results when examined in 
the hard cold light of modern statistical methods show unmistak- 
able evidence of being not entirely objective — of being biased in 
favour of the expected result ! 

The work of some psychologists on extrasensory perception 
and precognition may be a present-day example of a discovery 
before its time. Most scientists have difficulty in accepting the 
conclusions of these workers despite apparently irrefutable 
evidence, because the conclusions cannot be reconciled with 
present knowledge of the physical world. 

Unless made by someone outside accepted scientific circles, 
discoveries made when the time is ripe for them are more 
readily accepted because they fit into and find support in 
prevailing concepts, or indeed, grow out of the present body 
of knowledge. This type of discovery is bound to occur as part 



of the main current of the evolution of science and may arise 
more or less simultaneously in different parts of the world. 
Tyndall said : 

" Before any great scientific principle receives distinct enun- 
ciation by individuals, it dwells more or less clearly in the 
general scientific mind. The intellectual plateau is already high, 
and our discoverers are those who, like peaks above the plateau, 
rise a little above the general level of thought at the time." *^ 

Such discoveries, nevertheless, often encounter some resistance 

before they are generally accepted. 

There is in all of us a psychological tendency to resist new 
ideas which come from without just as there is a psychological 
resistance to really radical innovations in behaviour or dress. It 
perhaps has its origin in that inborn impulse which used to be 
spoken of as the herd instinct. This so-called instinct drives 
man to conform within certain limits to conventional customs 
and to oppose any considerable deviation from prevailing 
behaviour or ideas by other members of the herd. Conversely, 
it gives widely held beliefs a spurious validity irrespective of 
whether or not they are founded on any real evidence. Instinc- 
tive behaviour is usually rationalised, but the " reasons " are 
only secondary, being formed by the mind to justify its opinions. 

Wilfred Trotter said : 

" The mind likes a strange idea as little as the body likes a 
strange protein and resists it with similar energy. It would not 
perhaps be too fanciful to say that a new idea is the most quickly 
acting antigen known to science. If we watch ourselves honestly 
we shall often find that we have begun to argue against a new 
idea even before it has been completely stated."^* 

When adults first become conscious of something new they 
usually either attack or try to escape from it.'*^ This is called 
the " attack-escape " reaction. Attack includes such mild forms 
as ridicule, and escape includes merely putting out of mind. 
The attack on the first man to carry an umbrella in London 
was an exhibition of the same reaction as has so often been 
displayed toward startling new discoveries in science. These 
attacks are often accompanied by rationalisations — the attacker 
giving the " reasons " why he attacks or rejects the idea. Scepti- 
cism is often an automatic reaction to protect ourselves against 



a new idea. How often do we catch ourselves automatically 
resisting a new idea someone presents to us. As Walshe says, 
the itch to suffocate the infant idea bums in all of us.^°^ 

Dale describes the ridicule which greeted Rontgen's first 
announcement of his discovery of X-rays.^^ An interesting 
feature of the story is that the great physicist J. J. Thomson 
did not share in the general scepticism, but on the contrary 
expressed a conviction that the report would prove to be true. 
Similarly, when Becquerel's discovery that uranium salts emitted 
radiations was announced, Lord Rayleigh was prepared to 
believe it while others were not. Thomson and Rayleigh had 
minds that were not enslaved by current orthodox views. 

Some discoveries have had to be made several times before 
they were accepted. Writing of the resistance to new ideas 
Schiller says : 

" One curious result of this inertia, which deserves to rank 
among the fundamental ' laws ' of nature, is that when a dis- 
covery has finally won tardy recognition it is usually found to 
have been anticipated, often with cogent reasons and in great 
detail. Darwinism, for instance, may be traced back through the 
ages to Heraclitus and Anaximander."^" 

It is not uncommon for opponents of an innovation to base 
their judgment on an " all or nothing " attitude, i.e., since it 
does not provide a complete solution to the practical problem, 
it is no use. This unreasonable attitude sometimes prevents or 
delays the adoption of developments which are very useful in 
the absence of anything better. We all know some scientists who 
steadfastly refuse to be convinced by the evidence in support 
of a discovery which conflicts with their preconceived ideas. 
Perhaps the persistent sceptic serves a useful purpose in the 
community, but I admit that it is not one which I admire. It is 
said that even today there are some people who still insist that 
the world is flat ! 

Nevertheless, exasperating and even harmful as resistance to 
discovery often is, it fulfils a function in buffering the community 
from the too hasty acceptance of ideas until they have been 
well proved and tried. But for this innate conservatism, wild 
ideas and charlatanry would be more rife than they are. Nothing 
could be more damaging to science than the abandonment of 



the critical attitude and its replacement by too ready acceptance 
of hypotheses put forward on slender evidence. The 
inexperienced scientist often errs in being too willing to believe 
plausible ideas. Superficially one's reaction to a new claim 
appears to be an example of the general problem of conservatism 
versus progressiveness. These attitudes of mind may sub- 
consciously influence a person toward taking one side or the 
other in a dispute but we should strive against both of them, 
what we must aim at is honest, objective judgment of the 
evidence, freeing our minds as much as possible from opinion 
not based on fact, and suspend judgment where the evidence 
is incomplete. There is a very important distinction between 
a critical attitude of mind (or critical " faculty ") and a sceptical 

Opposition to discoveries 

Hitherto we have been concerned with psychological resistance 
to new ideas. In this section we will discuss some other aspects 
of opposition to discoveries. 

Innovations are often opposed because they are too disturbing 
to entrenched authority and vested interests in the widest sense 
of that term. Zinsser quotes Bacon as saying that the dignitaries 
who hold high honours for past accomplishments do not usually 
like to see the current of progress rush too rapidly out of their 
reach. Zinsser comments : 

" Our task, as we grow older in a rapidly advancing science, is 
to retain the capacity of joy in discoveries which correct older 
ideas, and to learn from our pupils as we teach them. That is the 
only sound prophylaxis against the dodo-disease of middle 

Trouble over innovations is sometimes aggravated by the 
personality of the discoverer. Discoverers are often men with 
little experience or skill in human relations, and less trouble 
would have arisen had they been more diplomatic. The fact 
that Harvey succeeded eventually in having his discovery 
recognised, and that Semmelweis failed, may be explained on 
this basis. Semmelweis showed no tact at all, but Harvey 
dedicated his book to King Charles, drawing the parallel between 
the King and realm, and the heart and body. His biographer, 

1 1 1 


Willis, says he possessed in a remarkable degree the power of 
persuading and conciliating those with whom he came in contact. 
Harvey said : 

" Man comes into the world naked and unarmed, as if nature 
had destined him for a social creature and ordained that he 
should live under equitable laws and in peace; as if she had 
desired that he should be guided by reason." 

In discussing his critics he remarked : 

" To return evil speaking with evil speaking, however, I hold 
to be unworthy in a philosopher [i.e. scientist] and searcher 
after the truth." *°^ 

Writing on the same subject Michael Faraday said : 

" The real truth never fails ultimately to appear : and opposing 
parties, if wrong, are sooner convinced when replied to for- 
bearingly than when overwhelmed."^^ 

The discoverer requires courage, especially if he is young and 
inexperienced, to back his opinion about the significance of his 
finding against indifferences and scepticism of others and to 
pursue his investigations. We take joy in reading of the courage 
displayed by men like Harvey, Jenner, Semmelweis and Pasteur 
in the face of opposition, but how often have profitable lines 
of investigation been dropped and lost in oblivion when the 
discoverer lacked the necessary zeal and courage ? Trotter relates 
the story of J. J. Waterston who in 1845 wrote a paper on the 
molecular theory of gases anticipating much of the work of 
Joule, Clausius and Clerk Maxwell. The referee of the Royal 
Society to whom the paper was submitted said : " The paper is 
nothing but nonsense ", and the work lay in utter obhvion until 
exhumed forty-five years later. Waterston lived on disappointed 
and obscure for many years and then mysteriously disappeared 
leaving no sign. As Trotter remarks, this story must strike a 
chill upon anyone impatient for the advancement of knowledge. 
Many discoveries must have thus been stillborn or smothered at 
birth. We know only those that survived. 

Although in most countries to-day there is no risk attached to 
pursuing what are now orthodox scientific fields, it would be 
wrong to conclude that obscurantism and reaction are things 
only of the past. Barely thirty years ago Einstein suffered a 
virulent and organised campaign of persecution and ridicule 

1 12 


in Germany*^ and in U.S.A. in 1925, at the notorious "Tennes- 
see monkey trial ", a science teacher was prosecuted for teaching 
evolution. In totalitarian states, the intrusion of poHtics into 
scientific matters, as was seen under the Nazi regime and now 
in Russia over the genetics controversy, may introduce authori- 
tarianism into science with consequent suppression of the work 
of those not willing to bow to the party dictum on scientific 
theories.^ A mild form of reaction persists in societies devoted 
to combating vaccination and vivisection. Nor should we 
scientists ourselves be too complacent, for even within scientific 
circles to-day a new discovery may be ignored or opposed if it 
is revolutionary in principle and made by someone outside 
approved circles. The discoverer may still be required to show 
the courage of his convictions. 

It has been said that the reception of an original contribution 
to knowledge may be divided into three phases : during the first 
it is ridiculed as not true, impossible or useless; during the 
second, people say there may be something in it but it would 
never be of any practical use; and in the third and final phase, 
when the discovery has received general recognition, there are 
usually people who say that it is not original and has been 
anticipated by others.* Theobald Smith spoke truly when he 
said : 

" The joy of research must be found in doing, since every other 
harvest is uncertain."®* 

It is a commonplace that in the past the great scientists have 
often been rewarded for their gifts to mankind by persecution. 
A good example of this curious fact is provided by the following 
story of what happened to Ignaz Semmelweis, when he showed 
how the dreadful suffering and loss of life due to puerperal fever 
that was then the rule in the hospitals of Europe could be pre- 

In 1847 Semmelweis got the idea that the disease was carried 
to the women on the hands of the medical teachers and students 
coming direct from the post-mortem room. To destroy the 
*' cadaveric material" on the hands he instituted a strict routine 

* This saying seems to have originated from Sir James Mackenzie {The 
Beloved Physician, by R. M. Wilson, John Murray, London). 


of washing the hands in a solution of chlorinated lime before 
the examination of the patients. As a result of this procedure, 
the mortality from puerperal fever in the first obstetric clinic of 
the General Hospital of Vienna fell immediately from 12 per 
cent to 3 per cent, and later almost to i per cent. His doctrine 
was well received in some quarters and taken up in some 
hospitals, but such revolutionary ideas, incriminating the 
obstetricians as the carriers of death, roused opposition from 
entrenched authority and the renewal of his position as assistant 
was refused. He left Vienna and went to Budapest where he 
again introduced his methods with success. But his doctrine 
made little headway and was even opposed by so great a man 
as Virchow. He wrote a book, the famous Etiology, to-day 
recognised as one of the classics of medical literature; but then 
he could not sell it. Frustration made him bitter and irascible 
and he wrote desperate articles denouncing as murderers those 
who refused to adopt his methods. These met only with ridicule 
and finally he came to a tragic end in a lunatic asylum in 1865. 
Mercifully and ironically a few days after entering the asylum 
he died from an infected wound received in the finger during 
his last gynaecological operation : a victim of the infection to 
the prevention of which his whole life had been devoted. His 
faith that the truth of his doctrine would ultimately prevail 
was never shaken. In a rather pathetic foreword to his Etiology 
he wrote : 

" When I look back upon the past, I can only dispel the sad- 
ness which falls upon me by gazing into that happy future when 
the infection will be banished. But if it is not vouchsafed to me 
to look upon that happy time with my own eyes . . . the convic- 
tion that such a time must inevitably sooner or later arrive will 
cheer my dying hour." 

The work of others, especially Tamier and Pasteur in 
France and Lister in England, forced the world reluctantly to 
recognise, some ten years or more later, that what Semmelweis 
had taught was correct. 

Semmelweis' failure to convince most people was probably 
because there was no satisfactory explanation of the value of 
disinfecting hands until bacteria were shown to be the cause of 
disease, and probably also because he did not exercise any 

1 14 


diplomacy or tact. It is not clear that Semmelweis' efforts had 
much, or indeed any, influence on the final acceptance of the 
principles he discovered. Others seem to have solved the problem 

Errors of interpretation 

For want of a more appropriate place, I shall mention here 
some of the commoner pitfalls which are encountered in inter- 
preting observations or experimental results and which have 
not already been discussed. 

The most notorious source of fallacy is probably post hoc, 
ergo propter hoc, that is, to attribute a causal relationship 
between what has been done and what follows, especially to 
conclude in the absence of controls that the outcome has been 
influenced by some interference. All our actions and reason 
are based on the legitimate assumption that all events have their 
cause in what has gone before, but error often arises when we 
attribute a causal role to a particular preceding event or inter- 
ference on our part which in reality had no influence on the 
outcome observed. The faith which the lay public has in 
medicines is due in a large measure to this fallacy. Until very 
recently the majority of medicines were of negligible value and 
had little or no influence on the course of the illness for which 
they were taken, nevertheless, many people firmly believed when 
they recovered that the medicine had cured them. A lot of people 
including some doctors, are convinced that certain bacterial 
vaccines prevent the common cold, because by a fortunate coinci- 
dence some patients had no cold the year following vaccination. 
Yet all the many controlled experiments done with similar 
vaccines failed to show the least benefit. The controlled experi- 
ment is the only way of avoiding this type of fallacy. 

Much the same logical fallacy is involved in wrongly assuming 
that when an association between two events is demonstrated, 
the relationship is necessarily one of cause and effect. Sometimes 
data are collected which show that the incidence of a certain 
disease in a quarter of a city which is very smoky, or which 
is very low-lying, is much higher than in other quarters. The 
author may conclude that the smoke or low-lying ground pre- 
disposes to the disease. Often such conclusions are quite 



unjustified, and the cause should probably be sought in the 
poverty and overcrowding which is to be found in these 
insalubrious areas. Virchow, in refuting Semmelweis' doctrine 
about the causation of puerperal fever, asserted that the 
weather played an important part, because the highest incidence 
occurred in winter. Semmelweis replied that the association 
between epidemics and winter was due to the fact that it was in 
winter that the midwifery students spent most time on the dis- 
section of dead bodies. 

False conclusions can be drawn by attributing a causal role 
to a newly introduced factor whereas, in fact, the cause lies in 
the withdrawal of the factor which was replaced. Tests carried 
out among people accustomed to drinking coffee at night could 
show that a better night's sleep was obtained when a proprietary 
drink was taken instead of coffee. It might be claimed that the 
proprietary drink induced sleep whereas the better sleep might 
well be entirely due to coffee not having been taken. Similarly, 
false conclusions in dietetic experiments have sometimes been 
drawn when a new constituent has replaced another. The 
supposed effect of the new constituent has later proved to be 
due to the absence of the article of diet displaced. It was 
found that the blooming of some plants was influenced by 
supplementing day light with artificial light. At first this was 
thought to be due to the prolonged " day ", but subsequently 
it was found to be due to the shortened " night ", for breaking 
into the night with a brief period of illumination at midnight, 
was even more effective than a longer period of illumination 
near the evening or morning. 

There is always a risk in applying conclusions reached from 
experimentation in one species, to another species. Many 
mistakes were made in concluding that man or a domestic 
animal required this or that vitamin because rats or other 
experimental animals did, but nowadays the error of this is 
generally appreciated. More recently the same trouble arose in 
chemotherapy. The sulphonamides which gave the best results 
in man were not always found to be the best against the same 
bacteria in some of the domestic animals. 

A rather more insidious source of fallacy is failure to realise 
that there may be several alternative causes of one process. 



W. B. Cannon^^ comments on the false deduction once made 
that adrenahne does not play a part in controlUng the sugar 
level in the blood by calling forth sugar from the liver, on the 
ground that the blood-sugar level is maintained after removal 
of the adrenal medulla. The fact is that there are other methods 
of mobilising sugar reserves from the liver but none are so 
effective as adrenaline. Shivering by itself can prevent body 
temperatures from falUng, but that does not prove that other 
processes cannot play a part. A variant of this " fallacy of a 
single cause " has been described by Winslow.^*"^ When a 
combination of two factors causes something, and one is 
universally present, it is usually rashly concluded that the other 
is the sole causal factor. In the nineteenth century it was 
believed that insanitary conditions in themselves caused enteric 
fever. The causal microbes were then universally present and 
the incidence of the disease was determined by presence or 
absence of sanitation. The cause of a disease is complex, 
consisting of a combination of causal microbe, the conditions 
necessary for its conveyance from one host to the next and 
factors affecting the susceptibility of the host. Any happening is 
the result of a complex of causal factors, one of which we usually 
single out as the cause owing to its not being commonly present 
as are the other circumstances. 

Wrong conclusions about the incidence of some condition 
in a population are sometimes drawn through basing the observa- 
tions on a section of the population which is not representative 
of the whole. For example, certain figures were generally 
accepted and printed in text-books as an index of the proportion 
of children at different ages that gave a negative reaction to 
the Schick test for immunity to diphtheria. Many years later 
these figures were found to be true only for children of the 
poorer classes attending public hospitals in the city. The figures 
for other sections of the population were very different. When 
I went to the U.S.A. in 1938, scarcely anyone I met could say 
a good word for President Roosevelt, but Dr. Gallup's method 
of sampling public opinion showed that more than fifty per cent 
supported him. There is a great temptation to generalise on 
one's own observations or experience, although often it is not 
based on a sample that is truly random or sufficiently large to 



be representative. Bacon warned against being led into error 
by relying on impressions. 

" The human understanding is most excited by that which 
strikes and enters the mind at once and suddenly, and by which 
the imagination is immediately filled and inflated. It then begins 
almost imperceptibly to conceive and suppose that everything is 
similar to the few objects which have taken impression on the 

A very common way in which mistakes arise is by making 
unjustified assumptions on incomplete evidence. To cite a 
classic example, in the lecture in which he enunciated his famous 
postulates, Robert Koch described how he had been led into 
error by making what appeared to be a reasonable assumption. 
In his pioneer work on the tubercle bacillus he obtained strains 
from a large variety of animal species and after having subjected 
them to a series of tests he concluded that all tubercle bacilli 
are similar. Only in the case of the fowl did he omit to do 
pathogenicity and cultural examinations because he could not 
at the time obtain fresh material. However, since the morphology 
was the same, he assumed that the organism from the fowl was 
the same as those from the other animals. Later he was sent 
several atypical strains of the tubercle bacillus which, despite 
a protracted investigation, remained a complete puzzle. He said : 

" When every attempt to discover the explanation of the dis- 
crepancy had failed, at length an accident cleared up the 

He happened to get some fowls with tuberculosis and when 
he cultured the organisms from these : 

" I saw to my astonishment that they had the appearance and 
all the other characters of the mysterious cultures." 

Thus it was he found that avian and mammalian tubercle 
bacteria are different. ^^ Incidentally, this reference, which I 
found when looking for something else, seems to have been 
" lost ", for some current text-books state that there is no evidence 
that Koch ever put forward the well-known postulates contained 
in this lecture. 

One can easily be led astray when attempting to isolate an 
infective agent by inoculation and passage in experimental 



animals. Many mice carry in their nose latent viruses which, 
when any material is inoculated into the lungs through the nose, 
are carried into the lungs where they multiply. If the lungs 
from these mice are used to inoculate other mice in the same 
way, pneumonia is sometimes set up and, as a result, it might 
be wrongly concluded that a virus had been isolated from the 
original material. Also in attempting to isolate a virus by 
inoculating material on to the skin of experimental animals, it 
is possible to set up a transmissible condition which originated 
from the environment and not from the original inoculum. 

Early investigations on distemper of dogs incriminated as the 
causal agent a certain bacterium isolated from cases of the 
disease because on inoculation it set up a disease resembling 
distemper. When later a virus was shown to be the true cause 
of the distemper, it became apparent that the early investigators 
had been misled either because they had isolated a pathogenic 
secondary invader or because they had not taken sufficiently rigid 
measures to quarantine their experimental dogs. 

When the investigator has done his best to detect any errors 
in his work, a service that colleagues are usually glad to assist 
with is criticism. He is a bold man who submits his paper for 
pubUcation without it having first been put under the microscope 
of friendly criticism by colleagues. 


The mental resistance to new ideas is partly due to the fact 
that they have to displace established ideas. New facts are not 
usually accepted unless they can be correlated with the existing 
body of knowledge; it is often not sufficient that they can be 
demonstrated on independent evidence. Therefore premature 
discoveries are usually neglected and lost. An unreasoning, 
instinctive mental resistance to novelty is the real basis of excessive 
scepticism and conservatism. 

Persecution of great discoverers was due partly to mental 
resistance to new ideas and partly to the disturbance caused to 
entrenched authoritv and vested interests, intellectual and 
material. Sometimes lack of diplomacy on the part of the 
discoverer has aggravated matters. Opposition must have killed 



at birth many discoveries. Obscurantism and authoritarianism 
are not yet dead. 

Included among the many possible sources of fallacy are 
post hoc, ergo propter hoc, comparing groups separated by time, 
assuming that when two factors are correlated the relationship 
is necessarily one of cause and effect, and generalising from 
observations on samples that are not representative. 




" Work, Finish, Publish." — Michael Faraday. 

Planning and organising research 

MUCH controversy has taken place over planning in research. 
The main disagreement is on the relative merits of pure 
and applied research, on what proportion of the research in a 
country should be planned and to what degree it should be 
planned. The extreme advocates of planning consider that the 
only research worth while is that which is undertaken in a 
deliberate attempt to meet some need of society, and that pure 
research is seldom more than an elegant and time-wasting 
amusement. On the other hand the anti-planners (in England 
there is a Society for Freedom in Science) maintain that the 
research worker who is organised becomes only a routine 
investigator because, with the loss of intellectual freedom, 
originality cannot flourish. 

Discussions on planning research are often confused by failure 
to make clear what is meant by planning. It is useful to dis- 
tinguish three different levels of planning. The first is the 
actual conduct of an investigation by the worker engaged in 
the problem. This corresponds with tactics in warfare. It is 
short term and seldom goes far beyond the next experiment. 
The second level involves planning further ahead on broad lines 
and corresponds with strategy in warfare. Planning at this level 
is not confined to the man engaged in the problem but is also 
often the concern of the research director and the technical 
committee. Finally there is planning of policy. This type of 
planning is mostly done by a committee which decides what 
problems should be investigated and what projects or workers 
should receive support. 

It has already been pointed out that many discoveries are 



quite unforeseen, and that the principal elements in biological 
research are intensely individual efforts in (a) recognising the 
unexpected discovery and following it up, and {b) concentrated 
prolonged mental effort resulting in the birth of ideas. Major 
discoveries probably result less frequently from the systematic 
accumulation of data along planned lines. It is not a fact, as 
some suppose, that no solution to a problem is likely to be 
found until we have fundamental knowledge on the subject. 
Frequently an empirical discovery is made providing a solution 
and the rationale is worked out afterwards. One of the 
principal morals to be drawn from the discoveries described in 
this book is that the research worker ought not, having decided 
on a course of action, to put on mental blinkers and, like a cart- 
horse, confine his attention to the road ahead and see nothing by 
the way. 

In view of these lessons which are to be learnt from the 
history of scientific discovery, research is less likely to 
be fruitful where the investigation is planned at the tactical 
level by a committee than when the person actually doing the 
research works out his own tactics as the investigation unfolds. 
Research is for most workers an individualistic thing and the 
responsibility for tactical planning is best left to the individual 
workers, who will devote their mental energies to the subject if 
they are allowed the incentives and rewards that are essential 
for fruitful research. Initiative can be easily discouraged by too 
much supervision for a man will seldom put his whole heart 
into a problem unless he feels that it is his own. Simon Flexner, 
the founder of the Rockefeller Institute of Medical Research, 
always believed that men of the right sort could be trusted to 
have better ideas than others could think up for them." The 
scientist should not even be expected to adhere in detail to a 
programme of work which he himself has drawn up, but should 
be allowed to vary it as developments require. 

The late Professor W. W. C. Topley said : 

" Committees are dangerous things that need most careful 
watching. I believe that a research committee can do one useful 
thing and one only. It can find the workers best fitted to attack 
a particular problem, bring them together, give them the facilities 
they need, and leave them to get on with the work. It can review 



progress from time to time, and make adjustments; but if it 
tries to do more, it will do harm."^^ 

Technical committees and research directors can often help 
in planning at the strategic level providing they work in consulta- 
tion with the man who is going to do the work and do not 
attempt to dictate tactics. Committees are of most value in 
planning at the poUcy level, in calling attention to problems of 
importance to the community and making available the necessary 
finances and scientists. Another useful function that a com- 
mittee can sometimes perform is to accelerate advances by seeing 
that workers in different laboratories are kept informed of each 
other's progress without the usual delay entailed in publication. 
Some war-time committees did useful service in co-ordinating 
scattered work in this way. 

It is perhaps so obvious as to be scarcely worth mentioning 
that planning at the strategic and poUcy levels places a heavy 
responsibiUty on the planners, and is only likely to be successful 
when entrusted to people who have a real understanding of 
research as well as a good general knowledge in science. It is 
generally recognised that a committee which draws up pro- 
grammes of research at the strategic level should consist mainly 
of men actively engaged in the field of research in which the 
problem falls. Unfortunately often committees are too incUned to 
play safe and support only projects which are planned in detail 
and follow conventional lines of work. Worthwhile advances are 
seldom made without taking risks. 

Plans and projects are in order for tackling recognised 
problems, that is to say, for applied research, but science also 
needs the independent worker who pursues pure research without 
thought of practical results. 

In team work some individual or individuals should usually 
take the lead and do the thinking. There are, of course, some 
scientists who are not well fitted to do independent research 
and yet who may be very useful working under close direction 
as members of a team. Other things being equal, the person 
with a fertile imagination makes a better leader than someone 
with a purely logical mind, for the former is more inspiring as 
well as more useful in providing ideas. But the leader of 
a team needs to be actively engaged on the problem himself. 



In Other words the tactical planning is best done by the bench 
worker, not the office administrator. Where there is not an 
acknowledged leader of the team, the problem can often be 
divided up so that each person capable of independent work 
has his own aspect of the problem for which he is responsible. 
The thing to avoid is too detailed and rigid planning by the 
assembled team. However, when team work is undertaken, the 
work ought to be sufficiently co-ordinated for each to understand 
not only his own special aspect but have a good grasp of the 
problem as a whole. The principles of team work were well 
expressed by Ehrlich : " Centralisation of investigation with 
independence of the individual worker." All plans must be 
regarded as tentative and subject to revision as the work pro- 
gresses. One must not confuse the planning of research with the 
planning of individual experiments. No one would dispute the 
advisability of devoting great care to the planning of experi- 
ments and carrying them through according to plan. 

Team work is essential in research in the investigation of 
problems which overlap into several branches of science, for 
instance, the investigation of a disease by a clinician, bacteriolo- 
gist and biochemist. Large teams are most frequently used in 
biochemical investigations where there is need for a large amount 
of co-ordinated skilled technical work. Also team work is often 
required to develop discoveries which have originated from 
individual workers. 

Another important use of the team is to increase the capacity 
of the brilliant man beyond what he could do with only his 
hands and technical assistance. The research team, especially 
of this type, also is valuable in providing an opportunity for 
the beginner to learn to do research. The young scientist benefits 
more from working in collaboration with an experienced research 
worker than by only having supervision from him. Also in this 
way he is more likely to get a taste of success, which is a 
tremendous help. Moreover, the association of the freshness 
and originality of youth with the accumulated knowledge and 
experience of a mature scientist can be a mutually beneficial 
arrangement. Where close collaboration is involved, the personali- 
ties of the individuals are, of course, an important consideration. 
Most brilliant men are stimulating to others, but some are so 



full of ideas from their own fertile mind and are so keen to 
try them out that they have a cramping effect on a junior 
colleague who wants to try out his own ideas. Moreover, it is 
possible for a man to be a brilliant scientist and yet be quite 
undeveloped in the knowledge and practice of human personal 

The objection most often raised against team work is that 
those discoveries which arise from unexpected side issues will 
be missed if the worker is not free to digress from his investiga- 
tion. Reming has pointed out that had he been working in 
a team he would not have been able to drop what he was doing 
and follow the clue that led to penicillin.*^ 

For his own guidance the research worker himself needs to 

make at least some tentative general plan of an investigation 

at the outset and to make very careful detailed plans for actual 

experiments. It is here that the experience of the research 

director can be most helpful to the young scientist. The latter 

presents for discussion a general picture of the information he 

has collected, together with his ideas for the proposed work. The 

inexperienced scientist usually does not realise the limitations 

of what is practicable in research, and often proposes for one 

year's work a plan that would occupy him for ten. The 

experienced man knows that it is a practical necessity to confine 

himself to a fairly simple project because he realises how much 

work even that entails. From hearing of only the successful 

investigations the uninitiated often gets a false idea of the 

easiness of research. Advances are nearly always slow and 

laborious and one person can attempt only a limited objective 

at a time. It is as well for the beginner to discuss with his 

supervisor any important deviations from the plan because 

although fruitful clues may arise which should be followed, it 

is neither possible nor desirable to pursue every unanswered 

question that comes up. To give advice on these issues and to 

help when difficulties are met are the main functions of a 

director of research, and the successes of those under his direction 

are a measure of his understanding of the nature of scientific 

investigation. As the young scientist develops he should be 

encouraged to become less and less dependent on his seniors. 

The rate at which this independence develops will be deter- 



mined by the aptitude that he shows and the success he attains. 

Both the team worker and the individual worker usually find 
it useful to keep a list of the ideas and experiments he intends 
to try — a work programme, which is revised continuously. 

Some consider that the best work is done in small research 
institutes where the director can keep in intimate touch with 
all the work, and that when this size is passed efficiency drops. 
It is undoubtedly true that there are examples of small institutes 
whose output per man is better than in the average large 
institute. In such places one usually finds a director who is not 
only a capable scientist but who also stimulates enthusiasm in 
his staff High productivity in large institutes perhaps depends 
on there being several active foci, each centred on a good leader. 

Different types of research 

Research is commonly divided into "applied" and "pure". 
This classification is arbitrary and loose, but what is usually 
meant is that applied research is a deliberate investigation of a 
problem of practical importance, in contradistinction to pure 
research done to gain knowledge for its own sake. The pure 
scientist may be said to accept as an act of faith that any 
scientific knowledge is worth pursuing for its own sake, and, 
if pressed, he usually claims that in most instances it is eventually 
found to be useful. Most of the greatest discoveries, such as 
the discovery of electricity, X-rays, radium and atomic energy, 
originated from pure research, which allows the worker to follow 
unexpected, interesting clues without the intention of achieving 
results of practical value. In applied research it is the project 
which is given support, whereas in pure research it is the man. 
However, often the distinction between pure and applied research 
is a superficial one as it may merely depend on whether or not 
the subject investigated is one of practical importance. For 
example, the investigation of the life cycle of a protozoon in a 
pond is pure research, but if the protozoon studied is a parasite 
of man or domestic animal the research would be termed applied. 
A more fundamental differentiation, which corresponds only very 
roughly with the applied and pure classification is {a) that in 



which the objective is given and the means of obtaining it are 
sought, and {b) that in which the discovery is first made and then 
a use for it is sought. 

There exists in some circles a certain amount of intellectual 
snobbery and tendency to look disdainfully on applied investiga- 
tion. This attitude is based on the following two false ideas : 
that new knowledge is only discovered by pure research while 
applied research merely seeks to apply knowledge already avail- 
able, and that pure research is a higher intellectual activity 
because it requires greater scientific ability and is more difficult. 
Both these ideas are quite wrong. Important new knowledge has 
frequently arisen from applied investigation; for instance, the 
science of bacteriology originated largely from Pasteur's investiga- 
tions of practical problems in the beer, wine and silkworm 
industries. Usually it is more difficult to get results in applied 
research than in pure research, because the worker has to stick 
to and solve a given problem instead of following any promising 
clue that may turn up. Also in applied research most fields have 
already been well worked over and many of the easy and 
obvious things have been done. Applied research should not be 
confused with the routine practice of some branch of science 
where only the application of existing knowledge is attempted. 
There is need for both pure and applied research for they tend 
to be complementary. 

Practical problems very often require for their solution more 
than the mere application of existing knowledge. Frequently 
gaps in our knowledge are found that have to be filled in. 
Furthermore, if applied research is limited to finding a solution 
to the immediate problem without attempting to arrive at an 
understanding of the underlying principles, the results will 
probably be applicable only to the particular local problem and 
will not have a wide general application. This may mean that 
similar and related problems have to be investigated afresh, 
whereas had the original investigation been done properly it 
would have provided the solution to the others. Even an 
apparently simple matter such as the practical development of 
a discovery may present unsuspected difficulties. When the new 
insecticide, gammexane, was adopted for use as a sheep dipping 
fluid, very careful tests and field trials were conducted to deter- 



mine that it was non-toxic and in every way harmless. But despite 
its having passed an extensive series of tests, when it became 
widely used in the field, sheep in a number of flocks developed 
severe lameness after dipping. Investigation showed that the 
lameness was not due to the gammexane but to infection with 
a certain bacterium. The dipping fluid had become fouled with 
this bacterium which was carried in by some of the sheep. 
Dipping fluids used previously had a germicidal action against 
this bacterium, but gammexane had not. Problems of control in 
biology are often different in different localities. The malaria 
parasite may have as an intermediate host a different species 
of mosquito and the liver fluke may utilise a different snail. 

Applied research cuts horizontally across several pure sciences 
looking for newly found knowledge that can be used in the 
practical problem. However, the applied scientist is not content 
with waiting for the discoveries of the pure scientist, valuable 
as they are. The pure scientist leaves serious gaps in those aspects 
of the subject which do not appeal to him, and the applied 
scientist may have to initiate fundamental research in order to 
fill them. 

Scientific research may also be divided into the exploratory 
type which opens up new territory, and developmental type 
which follows on the former. The exploratory type is free and 
adventurous; occasionally it gives us great and perhaps 
unexpected discoveries; or it may give us no results at all. 
Developmental type of research is more often carried on by the 
very methodical type of scientist who is content to consolidate the 
advances, to search over the newly won country for more modest 
discoveries, and to exploit fully the newly gained territory by 
putting it to use. This latter type of research is sometimes spoken 
of as "pot-boiling" or "safety first" research. 

"Borderline" research is research carried on in a field where 
two branches of science meet. This can be very productive in 
the hands of a scientist with a sufficiently wide training because 
he can both use and connect up knowledge from each branch 
of science. A quite ordinary fact, principle or technique from 
one branch of science may be novel and fruitful when applied 
in the other branch. 

Research may be divided into different levels which are reached 



successively as a branch of science or a subject becomes more 
advanced. First comes the observational type of research carried 
out by naturalists in the field or by scientists with similar mental 
attributes in the laboratory. Gradually the crude phenomena and 
materials become refined to more precise but more restricted 
laboratory procedures, and these ultimately are reduced to exact 
physical and chemical processes. It is almost a practical impossi- 
bility for anyone to have a specialist knowledge of more than a 
limited field at one level. The natural historian type, who is 
no less useful than his colleagues, owes most of his success to 
his powers of observation and natural wit and often lacks the 
depth of basic scientific knowledge necessary to develop his 
findings to the full. On the other hand, the specialist in a basic 
science may be too far removed, mentally and physically, from 
phenomena occurring in nature to be the equal of the natural 
historian type in starting new lines of work. 

The transfer method in research 

All scientific advances rest on a base of previous knowledge. 
The discoverers are the people who supply the keystone to 
another arch in the building and reveal to the world the com- 
pleted structure built mainly by others. In this section, however, 
I am referring not so much to the background of knowledge 
on which one tries to build but rather to the adaptation of a 
piece of new knowledge to another set of circumstances. 

Sometimes the central idea on which an investigation hinges 
is provided by the appHcation or transfer of a new principle 
or technique which has been discovered in another field. The 
method of making advances in this way will be referred to as 
the "transfer" method in research. This is probably the most 
fruitful and the easiest method in research, and the one most 
employed in appHed research. It is, however, not to be in any 
way despised. Scientific advances are so difficult to achieve that 
every useful stratagem must be used. Some of these contributions 
might be more correctly called developments rather than dis- 
coveries since no new principles and little new knowledge may be 
brought to light. However, usually in attempting to apply the 



newly discovered principle or technique to the different problem, 
some new knowledge does arise. 

Transfer is one of the principal means by which science evolves. 
Most discoveries have applications in fields other than those in 
which they are made and when applied to these new fields they 
are often instrumental in bringing about further discoveries. 
Major scientific achievements have sometimes come from transfer. 
Lister's development of antiseptic surgery was largely a transfer 
of Pasteur's work showing that decomposition was due to 

It might be thought that as soon as a discovery is announced, 
all its possible applications in other fields follow almost im- 
mediately and automatically, but this is seldom so. Scientists some- 
times fail to realise the significance which a new discovery in 
another field may have for their own work, or if they do realise it 
they may not succeed in discovering the necessary modifications. 
Years elapsed between the discovery of most of the principles of 
bacteriology and immunology and all their applications to various 
diseases. It was some time before the principle of haemagglutina- 
tion by viruses, discovered by Hirst with influenza virus, was 
found to hold with several other viruses, however with modifica- 
tions in some instances, as one might have expected, and still later 
it has been extended to certain bacteria. 

An important form of the transfer method is the exploitation 
of a new technique adopted from another branch of science. 
Some workers deliberately take up a new technique and look for 
problems in which its special virtues offer new openings. Partition 
chromatography and haemagglutination have, for example, been 
used in this way in fields far removed from those in which they 
were first developed. 

The possibility of developments by the transfer method is 
perhaps the main reason why the research man needs to keep 
himself informed of at least the principal developments taking 
place in more than his own narrow field of work. 

In this section we might also mention the scientific develop- 
ments of customs and practices already in use without any 
scientific background. A large number of drugs used in thera- 
peutics came into use in this way. Quinine, cocaine, curare and 
ephedrine were used long before they were studied scientifically 



and their pharmacological action understood. The medicinal pro- 
perties of the herb Ma Huang, from which ephedrine is derived 
are said to have been discovered in China, 5,000 years ago by the 
emperor Shen Nung. The discoveries of quinine, cocaine and 
curare by the natives in South America are lost in antiquity but 
obviously they must have been purely empirical. Incidentally, 
the tree from which quinine is obtained was named after the 
Countess of Cinchona who used it to cure malaria in 1638 and 
subsequently introduced it into Europe from Peru. Another 
example of this type of investigation is research into age-old 
processes such as tanning, cheese making and fermentation of 
various kinds. Many of these processes have now been developed 
into exact scientific procedures and thereby improved, or at least 
made more dependable. Vaccination could perhaps also be classi- 
fied under this heading. 


In order to examine and get a better understanding of a 
complex process, it is often useful to analyse it into component 
phases and consider each separately. This is what has been done 
in this treatise on research. I have tried to describe the role of 
hypothesis, reason, experimentation, observation, chance and 
intuition in research and to indicate the special uses and defects 
of each of these factors. However, in practice these factors 
of course do not operate separately. Several or all are usually 
required in any investigation, although often the actual key to 
the solution of the problem is provided by one, as is shown in 
many of the anecdotes cited. 

A general outline of how a straightforward problem in experi- 
mental medicine or biology may be tackled has been given in 
Chapters One and Two and the special role of each factor in 
research has been discussed in subsequent chapters. The order of 
the chapters has no special significance, nor does the space devoted 
to each subject bear much relationship to its relative importance. 
There remain to be discussed only some general considerations 
about tactics. In doing this it may be useful to recapitulate and 
bring together some of the points already made elsewhere. 

No set rules can be followed in research. The investigator has 



to exercise his ingenuity, originality and judgment and take 
advantage of every useful stratagem. F. C. S. Schiller wrote : 

" Methods that succeed must have value. . . . The success has 
shown that in this case the enquirer was right to select the facts 
he fixed upon as significant, and to neglect the rest as irrelevant, 
to connect them as he did by the ' laws ' he applied to them, to 
theorise about them as he did, to perceive the analogies, to 
weigh the chances, as he did, to speculate and to run the risks 
he did. But only in this case. In the very next case, which he 
takes to be * essentially the same ' as the last, and as nearly 
analogous as is humanly possible, he may find that the differences 
(which always exist between cases) are relevant, and that his 
methods and assumptions have to be modified to cope with it 

Research has been likened to warfare against the unknown. 
This suggests some useful analogies as to tactics. The first con- 
sideration is proper preparation by marshaUing all available 
resources of data and information, as well as the necessary 
material and equipment. The attacker will have a great advantage 
if he can bring to bear a new technical weapon. The procedure 
most likely to lead to an advance is to concentrate one's forces 
on a very restricted sector chosen because the enemy is believed 
to be weakest there. Weak spots in the defence may be found by 
preliminary scouting or by tentative attacks; when a stiff resis- 
tance is encountered it is usually better to seek a way around it 
by some manoeuvre instead of persisting in a frontal attack. 
Very occasionally, when a really important break-through is 
effected, it may be expedient, although risky, to overrun quickly 
a large territory and leave much of the consolidation to followers, 
provided the work is important enough to attract them. However, 
generally speaking, advances proceed by stages; when a new 
position is taken it should be firmly consoHdated before any 
attempt is made to use it as a base for further advance. This 
rhythm is the normal form of progression not only in scientific 
research but in all forms of scholarship : the gathering of 
information leads naturally to a pause for synthesis and interpreta- 
tion which in turn is followed by another stage of collection of 
crude data selected in light of the new generalisations reached. 
Even in applied research, such as the investigation of a disease 



of man or of domestic animals, the usual procedure is first to 
find out as much as possible about any or all of the aspects of 
the problem, without deliberately aiming at a particular objective 
of practical use. Experience has shown quite definitely that a 
fuller understanding of the subject nearly always reveals useful 
facts. Sometimes one finds a vulnerable link in the life-cycle of 
the parasite causing the disease and this may lead to a simple 
means of control. Having such a possibility in view it is helpful 
to consider the biology of the infective agent, whether it be virus 
or helminth, and to ponder on how it manages to survive, 
especially when making its way from one host to the next. 

Biological discoveries are often at first recognised in the form 
of qualitative phenomena and one of the first aims is usually to 
refine them to quantitative, reproducible processes. Eventually 
they may be reduced to a chemical or physical basis. It is note- 
worthy that the declared aim of a large proportion of investiga- 
tions described in the leading scientific journals is to disclose the 
mechanism of some biological process. It is a fundamental belief 
that all biological functions can eventually be explained in terms 
of physics and chemistry. Vitalism, which postulated mysterious 
" vital " forces, and teleology, which postulated a supernatural 
directing agency, have long ago been abandoned by experi- 
mental biologists. However, teleology is admissible in a modified 
sense that an organ or function fulfils a purpose toward aiding 
the survival of the organism as a whole or survival of the 

The most honoured and acclaimed advances in science are the 
perception of new laws and principles and factual discoveries 
of direct practical use to man. Usually little prominence is given 
to the inventions of new laboratory techniques and apparatus 
despite the fact that the introduction of an important new tech- 
nique is often responsible for a surge of progress just as much 
as is the discovery of a new law or fact. Solid media for the 
culture of bacteria, bacterial filters, virus haemagglutination and 
partition chromatography are outstanding examples. It may be 
profitable for research workers and the organisers of research to 
pay more attention to the developments of new techniques than 
has been the custom. 

It was a characteristic of Faraday, Darwin, Bernard and 



probably all great investigators to follow up their discoveries and 
not leave the trail till they had exhausted it. The story of 
Bernard's experiments with digestion in rabbits recounted earlier 
provides a good illustration of this poHcy. When Gowland 
Hopkins found that a certain test for proteins was due to the 
presence of glyoxylic acid as an impurity in one of the reagents, 
he followed this up to find what group in the protein it reacted 
with and this led to his famous isolation of tryptophane. Any 
new fact is potentially an important new tool to be used for 
uncovering further knowledge and a small discovery may lead 
to something much greater. As Tyndall said : 

" Knowledge once gained casts a faint light beyond its own 
immediate boundaries. There is no discovery so limited as not 
to illuminate something beyond itself." 


As soon as anything new is discovered the successful scientist 
immediately looks at it from all possible points of view and by 
connecting it with other knowledge seeks new avenues for investi- 
gation. The real and lasting pleasure in a discovery comes not so 
much from the accomplishment itself as from the possibility of 
using it as a stepping stone for fresh advances. 

Anyone with a spark of the research spirit does not need to be 
exhorted to chase for all he is worth a really promising clue when 
one is found, dropping for the time being other activities and 
interests as far as practicable. But in research most of the time 
progress is difficult and often one is up against what appears to 
be a " brick wall ". It is here that all resources of ingenuity and 
method are required. Perhaps the first thing to try is to abandon 
the subject for a few days and then reconsider the whole problem 
with a fresh mind. There are three ways in which benefit may 
be derived from temporary abandonment of a difficulty. It allows 
time for "incubation ", that is for the subconscious to digest the 
data, it allows time for the mind to forget conditioned thinking, 
and lastly, by not doggedly persisting, one avoids fixing too 
strongly the unprofitable lines of thought. The principle of 
temporary abandonment is, of course, widely practised in every- 
day life, as for example, in postponing the making of a difficult 
decision until one has " slept on it ". Elsewhere the usefulness 
of discussion has been stressed, not so much for seeking technical 



advice as for promoting new ideas. Also discussion helps one to 
gain that clear understanding of the problem, which is so essen- 

Another thing to try when one is up against an impasse is 
to go back to the beginning and try to find a new Hne of 
approach by looking at the problem in a different way. It may 
be possible to collect more data from the field or clinic. Fresh 
field or clinical observations may also be useful in prompting 
new ideas. As a result of trying to reduce the problem to an 
experimental inquiry, the worker may have selected a sterile and 
erroneous refinement of the problem. When the crude problem 
is seen again he may select some other aspect for investigation. 
Sometimes it is possible to resolve the difficulty into simpler 
components which can be tackled separately. If the difficulty 
cannot be overcome, perhaps a way around it can be found by 
using an alternative technical method. It may be helpful to look 
for analogies between the problem presented and others that have 
been solved. 

If, after persistent attempts to resolve the difficulty, no advance 
is being made, it is usually best to drop the problem for a few 
weeks or months and take up something else, but to think and 
talk about it occasionally. A new idea may arise or a new devel- 
opment in other fields may occur which enable the problem to be 
taken up again. If nothing fresh turns up, the problem will have 
to be abandoned as being insoluble in the present state of know- 
ledge in related fields. It is, however, a serious fault in a research 
worker to be too ready to drop problems as soon as he encoun- 
ters a difficulty or gets seized by enthusiasm for another line of 
work. Generally speaking one should make every effort to com- 
plete an investigation once it has been started. The worker who 
repeatedly changes his problem to chase his newest bright idea 
is usually ineffectual. 

As soon as a piece of work is nearing completion it should be 
written up as for publication. It is important to do this before 
the work has been brought to a close because frequently one 
finds gaps or weak points which can be remedied while the 
materials are still at hand. Even when the work is not nearing 
completion, it is as well to write up an investigation at least 
once a year, because otherwise when one writes up work from 



old notes, one's memory of the experiments has become dim so 
that the task is more difficult and cannot be done so well. Also, for 
reasons discussed elsewhere, it is desirable to review the problem 
periodically. However, work that has not produced significant 
results is better not published. It cluttei^s up the journals and 
does more harm than good to the author's reputation in the minds 
of the discerning. 

When the work has been completed, it is wise to submit the 
article to an experienced colleague for criticism — not only because 
the colleague may be more experienced than the author, but also 
because it is easier to see flaws in another's work or language than 
in one's own. 

A word of caution might be given against publishing work that 
is not conclusive and especially about making interpretations that 
are not fully justified by the experimental results or observations. 
Whatever is written will remain permanently in the literature and 
one's scientific reputation can be damaged by publishing some- 
thing that is later proved incorrect. Generally speaking, it is a 
safe policy to give a faithful record of the results obtained and 
to suggest only cautiously the interpretation, distinguishing 
clearly between facts and interpretation. Premature publication 
of work that could not be substantiated has at times spoilt the 
reputation of promising scientists. Superlatives and exaggeration 
are anathema to most scientists, the greatest of whom have 
usually been modest and cautious. Faraday wrote to a friend in 
1831 : 

" I am busy just now again on electro-magnetism, and think I 

have got hold of a good thing, but can't say. It may be a weed 

instead of a fish that, after all my labour, I may at last pull up." 

What he pulled up was the electric dynamo. In 1940 Sir Howard 
Florey wrote to the Rockefeller Foundation for financial sup- 
port for his work on penicillin, which he then had good reason 
for believing could be developed into a therapeutic agent even 
more effective than the sulphonamides. In such a letter one might 
be expected to present the work in the most favourable light, but 
this is all that Florey allowed himself to say : 

" I don't think I am too optimistic in thinking that this is a 
very promising line."'^ 

What a classic piece of understatement that has proved to be ! 



I confess that I did not read Bacon until after I had nearly 
finished writing this book and only then did I realise how clearly 
he had seen that discovery is more often than not empirical — the 
same view as I have reached from studying the methods which 
have produced results during recent times. He quotes with 
approval Celsus as saying : 

" That medicines and cures were first found out, and then after 
the reasons and causes were discoursed; and not the causes first 
found out, and by light from them the medicines and cures 

No more apt commentary could be made about the advances in 
chemotherapy of this century than this remark of Celsus' about 
the medical science of 1800 years ago. When one reflects that 
chance and empiricism is the method by which organic evolution 
developed, it is perhaps not so surprising that these factors play 
such an important part in biological research. 

In research we often have to use our techniques at their extreme 
limit and even beyond — like Schaudinn discovering the pale 
spirochaete of syphilis which others could barely see by the 
methods then available. So also with our reasoning; for usually 
discovery is beyond the reach of reason. 

In physics inductive logic is as inadequate as in biology. Ein- 
stein leaves us in no doubt on this point when he says : 

" There is no inductive method which could lead to the funda- 
mental concepts of physics. Failure to understand this fact 
constituted the basic philosophical error of so many investigators 
of the nineteenth century. . . . We now realise with special clarity, 
how much in error arcy those theorists who believe that theory 
comes inductively from experience." 

In formal education the student is implicitly, if not explicitly, 
led to believe that reason is the main, or even the only, means by 
which science advances. This view has been supported by the con- 
ception of the so-called " scientific method " outlined mainly by 
certain logicians of the last century who had little real under- 
standing of research. In this book I have tried to show the error 
of this outlook and have emphasised the limitations of reason 
as an instrument in making discoveries. I have not questioned the 
belief that reason is the best guide in known territory, though 



even here the hazards in its use are probably greater than gener- 
ally realised. But in research we are continually groping beyond 
known territory and here it is not so much a question of abandon- 
ing reason as finding that we are unable to employ it because 
there is not sufficient information available on which to use it 
properly. Rather than delude ourselves that we are able effec- 
tively to use reason in complex natural phenomena when we have 
only inadequate information and vague ideas, it seems to me 
better openly to recognise that we have often to resort to taste 
and to recognise the important roles of chance and intuition in 

In research, as indeed in everyday life, very often we have of 
necessity to decide our course of action on personal judgment 
based on taste. Only the technicalities of research are " scientific " 
in the sense of being purely objective and rational. Paradoxical 
as it may at first appear, the truth is that, as W. H. George has 
said, scientific research is an art, not a science."*^ 


Tactics are best worked out by the worker engaged on the 
problem. He should also have a say in planning strategy, but here 
he can often be assisted by a research director or by a technical 
committee which includes scientists familiar with the particular 
field of work. The main function of committees is planning 
matters of poUcy. Research can be planned but discovery 

When discoveries are transferred to another field of science 
they are often instrumental in uncovering still further knowledge. 
I have given some hints on how best to go about the various 
activities that constitute research, but explicit rules cannot be 
laid down because research is an art. 

The general strategy of research is to work with some clear 
object in view but nevertheless to keep alert for and seize any 
unexpected opportunities. 




" It is not the talents we possess so much as the use we 
make of them that counts in the progress of the world." 

Brailsford Robertson 

Attributes required for research 

IN MANY respects the research worker resembles the pioneer. 
He explores the frontiers of knowledge and requires many of 
the same attributes : enterprise and initiative, readiness to face 
difficulties and overcome them with his own resourcefulness and 
ingenuity, perseverance, a spirit of adventure, a certain dissatis- 
faction with well-known territory and prevailing ideas, and an 
eagerness to try his own judgment. 

Probably the two most essential attributes for the research 
worker are a love of science and an insatiable curiosity. The 
person attracted to research usually is one who retains more 
than usual of the instinct of curiosity. Anyone whose imagination 
cannot be fired by the prospect of finding out something never 
before found by man will only waste his and others' time by 
taking up research, for only those will succeed who have a genuine 
interest and enthusiasm for discovery. The most successful 
scientists are capable of the zeal of the fanatic but are discipUned 
by objective judgment of their results and by the need to meet 
criticism from others. Love of science is hkely to be accompanied 
by scientific taste and also is necessary to enable one to persist 
in the face of frustration. 

A good intelligence, internal drive, wiUingness to work hard 
and tenacity of purpose are further prerequisites for success in 
research, as in nearly all walks of life. The scientist also needs 
imagination so that he can picture in his mind how processes 
work, how things take place that cannot be observed and conjure 
up hypotheses. The research worker is sometimes a difficult person 



because he has no great confidence in his opinions, yet he also 
is sceptical of others' views. This characteristic can be incon- 
venient in everyday life. Cajal commenting on the importance 
of mental independence in the scientist, remarks that humility 
may be fitting for saints but seldom for scientists.^ ^" 

A spirit of indomitable perseverance has characterised nearly 
all successful scientists, for most worth while achievements re- 
quired persistence and courage in face of repeated frustrations. 
So strong was this trait in Darwin that his son said it went beyond 
ordinary perseverance and could better be described as dogged- 
ness. Pasteur said : 

" Let me tell you the secret that has led me to my goal. My 
only strength lies in my tenacity."^ ^^ 

People may be divided roughly into those who habitually 
react vigorously to external influences — including ideas — and 
those who are passive and accept things as they come. The 
former question everything they are told even as children and 
often rebel against the conventional. They are curious and want 
to find out things for themselves. The other type fits into life with 
less trouble and, other things being equal, more easily accumu- 
lates information given as formal teaching. The mind of this 
latter type becomes furnished with generally accepted ideas and 
set opinions, whereas the reactive type has fewer fixed opinions 
and his mind remains free and flexible. Of course, not everyone 
can be classed as belonging to one of these two extremes, but 
clearly those approximating to the passive type are not cut out 
for research. 

Preparing a list of the required attributes is not much help 
in the vexing problem of how to select promising people for 
research or of deciding yourself if you are suitable, because there 
is at present no objective means of measuring the qualities listed. 
However, this is a problem which psychologists might be able to 
solve in time. For example, it might be possible to devise a test 
of a person's knowledge of everyday things that would be a 
measure of his curiosity and powers of observation — his success 
in " discovering " things in his environment, for life can be a 
perpetual process of discovering. Tests might also be devised to 
measure ability to generalise, to formulate hypotheses to fit given 



data. Possibly love of science might be tested by determining the 
response — being delighted or not — on learning of scientific dis- 

Ordinary examinations are not a good guide to a student's 
ability at research, because they tend to favour the accumulators 
of knowledge rather than the thinkers. Brilliant examinees are 
sometimes no good at research, while on the other hand some 
famous scientists have made a poor showing at examinations. 
Paul Ehrlich only got through his final medical examinations by 
the grace of the examiners who had the good sense to give recog- 
nition to his special talents, and Einstein failed at the entrance 
examination to the Polytechnic School. Probably the student 
who is reflective and critical is at a disadvantage in accumulating 
information as compared with the student who accepts without 
question all he is told. Charles Nicolle goes so far as to say that 
the inventive genius is not able to store knowledge and that inven- 
tiveness may be killed by bad teaching, fixed ideas and erudition. ^^ 

I have noticed that in England a great many research workers 
in both the biological and non-biological sciences are, or have 
been in their youth, keen naturalists. The pursuing of some 
branch of natural history as a hobby by a young man may be a 
valuable indication of an aptitude for research. It shows that he 
gets pleasure from studying natural phenomena and is curious 
to find out things for himself by observation. 

At present the only way of selecting promising research talent 
— of " discovering discoverers " as Rous has put it — is by giving 
the candidate an opportunity of trying his hand at research for 
at least one or two years. Until the young scientist has shown that 
he has definite ability in research, it is wiser for him not to be 
given a permanent research position. This precaution is as 
important for the future welfare and happiness of the scientist 
as it is for the good of the research institution. It is helpful for 
undergraduates to be given an opportunity during their final 
year to dabble in research, as this often gives a preliminary indica- 
tion of a person's suitability for research. One favourable indica- 
tion is for the young graduate to show real desire to do research 
by taking steps to get a research position; in other words, the 
best research workers tend to select themselves. 

Whatever the exact mental requirements may be, it is a 



widely held opinion that not everyone is able to undertake 
research successfully, just as not everyone has talent for com- 
posing music, but lack of the particular requirements should not 
be regarded as a slur on the person's intelligence or his ability in 
other directions. 

Incentives and rewards 

The chief incentives of research are to satisfy curiosity, to 
satisfy the creative instinct, the desire to know whether one's 
conjecture has led to the creation of new knowledge and the 
desire for the feeling of importance by gaining recognition. 
More mundane incentives are the need to gain a livelihood and 
the ambition to "get on in the world", "showing" certain 
individuals who did not believe in your ability on the one hand, 
and on the other hand, trying to justify the confidence that others 
may have shown in you. Recognition of work done is an import- 
ant incentive as is illustrated by the ill-feeling sometimes dis- 
played over contentious points of priority in publication. Even 
great scientists are usually jealous of getting all due credit for 
their discoveries. The desire to see one's name in print and be 
credited throughout the scientific world with one's accomplish- 
ments is undoubtedly one of the most important incentives in 
research. In addition to these incentives which are common to all 
types of research, in applied research there is the desire to 
accomplish something for the good of mankind. This is likely to 
be more eflfective if it is not merely a vague ideal but if those 
to benefit are known to, or in some way associated with, the 
research worker. 

The man or woman with a research mind is fascinated by the 
mental challenge of the unexplained and delights in exercising 
the wits in trying to find a solution. This is just a manifestation 
of the phenomenon that many people find pleasure in solving 
problems, even when there is no reward attached, as is shown by 
the popularity of crossword puzzles and detective stories. In- 
cidentally Paul Ehrlich loved detective mysteries. Interest in a 
particular branch of science sometimes originates from the intrin- 
sic beauty of the material or technique employed. Naturalists 
and zoologists are often attracted to study a group of animals 
because they find their appearance pleasing and a bacteriologist 



may like using a certain technique because it appeals to his 
aesthetic sensibility. Very likely it was Ehrlich's extraordinary 
love of bright colours (he is said to have derived an ecstatic 
pleasure from them) that gave him an interest in dyes and so 
determined the direction in which his work developed. 

Albert Einstein distinguishes three types of research workers : 
those who take up science because it offers them an opportunity 
to exercise their particular talents and who exult in it as an 
athlete enjoys exercising his prowess; those who regard it as 
a means of livelihood and who but for circumstances might 
have become successful business men; and lastly the true 
devotees, who are rare but make a contribution to knowledge out 
of proportion to their numbers. ^^ 

Some psychologists consider that man's best work is usually 
done under adversity and that mental stress and even physical 
pain may act as a mental stimulant. Many prominent men have 
suffered from psychological troubles and various diflRculties but 
for which perhaps they would never have put forward that 
effort required to excel. 

The scientist seldom gets a large monetary reward for his 
labours so he should be freely granted any just fame arising 
from his work. But the greatest reward is the thrill of discovery. 
As many scientists attest, it is one of the greatest joys that life 
has to offer. It gives a tremendous emotional uplift and great 
sense of well-being and satisfaction. Not only factual discoveries 
but the sudden realisation of a generalisation can give the same 
feeling of exhilaration. As Prince Kropotkin wrote : 

" He who has once in his life experienced this joy of scientific 
creation will never forget it." 

Baker quotes the story of the great British biologist Alfred Wallace 
making a very small discovery : 

" None but a naturalist," wrote Wallace, " can understand the 
intense excitement I experienced when at last I captured it 
[a new species of butterfly]. My heart began to beat violently, 
the blood rushed to my head, and I felt much more like fainting 
than I have done when in apprehension of immediate death. I 
had a headache the rest of the day, so great was the excitement 
produced by what will appear to most people a very inadequate 




Referring to the elation he felt after demonstrating the feasibility 
of protecting people against smallpox by vaccination, Edward 
Jenner wrote : 

" The joy I felt at the prospect before me of being the instru- 
ment destined to take away from the world one of its greatest 
calamities . . . was so excessive that I sometimes found myself 
in a kind of reverie."^" 

Louis Pasteur and Claude Bernard made the following comments 
on this phenomenon : 

" When you have at last arrived at certainty, your joy is one 
of the greatest that can be felt by a human soul."^^ 

" The joy of discovery is certainly the liveliest that the mind of 
man can ever feel."^^ 

The discoverer has an urge to share his joy with his colleagues 
and usually rushes into a friend's laboratory to recount the event 
and have him come and see the results. Most people get more fun 
and enjoyment out of new developments if they are able to share 
them with colleagues who are working on the same subject or are 
sufficiently closely related to be genuinely interested. 

The stimulus of a discovery immediately wipes out all the 
disappointments of past frustrations and the scientist works with 
a new-found vigour. Furthermore, some stimulus is felt by his 
colleagues and so one discovery makes the conditions more pro- 
pitious for further advances. But unfortunately things do not 
always turn out like this. Only too often our joy is short-Uved 
and found to be premature. The consequent depression may be 
deep, and here a colleague can help by showing understanding 
and encouragement. To "take it" in this way without being 
beaten is one of the hard lessons the young scientist has to learn. 

Unfortunately research has more frustrations than successes 
and the scientist is more often up against what appears to be an 
impenetrable barrier than making progress. Only those who have 
sought know how rare and hard to find are those little diamonds 
of truth which, when mined and polished, will endure hard and 
bright. Lord Kelvin wrote : 

" One word characterises the most strenuous of the efforts for 
the advancement of science that I have made perseveringly 
during fifty-five years; that word is failure." 



Michael Faraday said that in the most successful instances less 
than one in ten of the hopes and preliminary conclusions are 
realised. When one is depressed, some cold comfort might be 
derived from the experience of those two great scientists. It is well 
for the young scientist to realise early that the fruits of research 
are not easily won and that if he is to succeed he will need 
endurance and courage. 

The ethics of research 

There are certain ethical considerations which are generally 
recognised among scientists. One of the most important is that, 
in reporting an investigation, the author is under an obligation 
to give due credit to previous work which he has drawn upon and 
to anyone who has assisted materially in the investigation. This 
elementary unwritten rule is not always followed as scrupulously 
as it should be and offenders ought to realise that increased credit 
in the eyes of the less informed readers is more than offset by the 
opprobrium accorded them by the few who know and whose 
opinion really matters. A common minor infringement that one 
hears is someone quoting another's ideas in conversation as though 
they were his own. 

A serious scientific sin is to steal someone's ideas or preliminary 
results given in the course of conversation and to work on them 
and report them without obtaining permission to do so. This is 
rightly regarded as little better than common thieving and I have 
heard a repeated offender referred to as a " scientific bandit ". 
He who transgresses in this way is not likely to be trusted again. 
Another improper practice which unfortunately is not as rare 
as one might expect, is for a director of research to annex most 
of the credit for work which he has only supervised by publishing 
it under joint authorship with his own name first. The author 
whose name is placed first is referred to as the senior author, 
but senior in this phrase means the person who was responsible 
for most of the work, and not he who is senior by virtue of the 
post he holds. Most directors are more interested in encouraging 
their junior workers than in getting credit themselves. I do not 
wish to infer that in cases where the superior officer has played 
a real part in the work he should withhold his name altogether, 



as over-conscientious and generous people sometimes do, but 
often it is best to put it after that of the younger scientist so 
that the latter will not be overlooked as merely one of "and 
collaborators". The inclusion of the name of a well known 
scientist who has helped in the work is often useful as a guarantee 
of the quality of the work when the junior author has not yet 
established a reputation for himself It is the duty of every 
scientist to give generously whatever advice and ideas he can 
and usually formal acknowledgment should not be demanded for 
such help. 

Some colleagues and myself have found that sometimes what 
we have thought to be a new idea turns out not to be original at 
all when we refer to notes which we ourselves made on the subject 
some time previously. Incomplete remembering of this type 
occasionally results in the quite unintentional annexing of another 
person's idea. An idea given by someone else in conversation may 
subsequently be recalled without its origin being remembered and 
thus be thought to be one's own. 

Complete honesty is of course imperative in scientific work. 
As Cramer said, 

" In the long run it pays the scientist to be honest, not only 
by not making false statements, but by giving full expression to 
facts that are opposed to his views. Moral slovenliness is visited 
with far severer penalties in the scientific than in the business 
world." 26 

It is useless presenting one's evidence in the most favourable light, 
for the hard facts are sure to be revealed later by other 
investigators. The experimenter has the best idea of the possible 
errors in his work. He should report sincerely what he has done 
and, when necessary, indicate where mistakes may have arisen. 

If an author finds out he cannot later substantiate some results 
he has reported he should publish a correction to save others either 
being misled or put to the trouble of repeating the work them- 
selves, only to learn that a mistake has been made. 

When a new field of work is opened up by a scientist, some 
people consider it courteous not to rush in to it, but to leave the 
field to the originator for a while so that he may have an 
opportunity of reaping the first fruits. Personally I do not see 
any need to hold back once the first paper has been published. 



Hardly any discovery is possible without making use of a 
knowledge gained by others. The vast store of scientific knowledge 
which is to-day available could never have been built up if 
scientists did not pool their contributions. The publication of 
experimental results and observations so that they are available 
to others and open to criticism is one of the fundamental 
principles on which modem science is based. Secrecy is contrary 
to the best interests and spirit of science. It prevents the individual 
contributing to further progress; it usually means that he or his 
employer is trying to exploit for their own gain some advance 
made by building on the knowledge which others have freely 
given. Much research is carried out in secret in industry and in 
government war departments. This seems to be inevitable in the 
world as it is to-day, but it is nevertheless wrong in principle. 
Ideally, freedom to publish, provided only that the work has 
sufficient merit, should be a basic right of all research workers. 
It is said that occasionally, even in agricultural research, results 
may be suppressed because they are embarrassing to government 
authorities.^^ This would seem to be a dangerous and shortsighted 

Personal secrecy in laboratories not subject to any restrictions 
is not infrequently shown by workers who are afraid that someone 
else will steal their preliminary results and bring them to fruition 
and publish before they themselves are able to do so. This form 
of temporary secrecy can hardly be regarded as a breach of 
scientific ethics but, although understandable, it is not commend- 
able, for free interchange of information and ideas helps hasten 
the advance of science. Nevertheless information given in confi- 
dence must be respected as such and not handed on to others. A 
travelling scientist visiting various laboratories may himself be 
perfectly honourable in not taking advantage of unpublished 
information he is given, but may inadvertently hand on such 
information to a less scrupulous individual. The traveller can best 
avoid this risk by asking not to be told anything that is wished 
to be kept confidential, for it is difficult to remember what is for 
restricted distribution and what not. 

Even in the scientific world, unfortunately, one occasionally 
encounters national jealousies. These are manifest by lack of 
appreciation or acknowledgment of work done in other countries. 



Not only is this to be deplored as a quite indefensible breach of 
ethics and of the international spirit of science, but it rebounds 
on the offenders, often to the detriment of themselves and their 
country. The person failing to appreciate advances in science 
made elsewhere may be left in the backwater he deserves, and 
he shows himself a second-rate scientist. Among the great majority 
of scientists there exists an international freemasonry that is one 
of the main reasons for faith in the future of mankind, and it is 
depressing to see this marred by petty selfishness on the part of a 
few individuals. 

Different types of scientific minds 

Not all minds work alike. Attempts are often made to divide 
scientists broadly into two types, but the classification is arbitrary 
and probably the majority fall somewhere between the two 
extremes and combine many of the characteristics of both. 

W. D. Bancroft,^" the American chemist, calls one type the 
" guessers " (using the word guess in the sense of making a shrewd 
judgment or hypothesis in advance of the facts) : these follow 
mainly the deductive or Aristotehan methods. They get their 
hypothesis first, or at any rate early in the investigation, and then 
test it by experiment. The other type he calls the "accumulators" 
because they accumulate data until the generalisation or hypo- 
thesis is obvious; these follow the inductive or Baconian method. 
However, the terms inductive and deductive, and Aristotelian 
and Baconian can be confusing and have sometimes been misused. 
Henri Poincare^^ and Jacques Hadamard^" classify mathemati- 
cians as either "intuitive" or "logical" according to whether 
they work largely by intuitions or by gradual systematic steps. 
This basis of classification seems to agree with Bancroft's. I will 
use the terminology "speculative" and "systematic" as this seems 
the simplest way of indicating the principal difference between 
the two types. 

Charles Nicolle®^ distinguished (a) the inventive genius who 
cannot be a storehouse for knowledge and who is not necessarily 
highly intelligent in the usual sense, and {b) the scientist with a 
fine intelligence who classifies, reasons and deduces but is, 
according to NicoUe, incapable of creative originality or making 



original discoveries. The former uses intuition and only calls on 
logic and reason to confirm the finding. The latter advances 
knowledge by gradual steps like a mason putting brick on brick 
until finally a structure is formed. Nicolle says that intuitions were 
so strong with Pasteur and Metchnikoff that sometimes they 
almost published before the experimental results were obtained. 
Their experiments were done mainly to reply to their critics. 
Bancroft gives the following illustrations of the outlook of the 
diflferent types of scientist. Examples of the systematic type are 
Kelvin and Sir W. Hamilton, who said, 

" Accurate and minute measurement seems to the non- 
scientific imagination a less lofty and dignified work than looking 
for something new, yet nearly all the grandest discoveries are 
made this way ", 

" In physical sciences the discovery of new facts is open to any 
blockhead with patience and manual dexterity and acute senses." 

Contrast this last statement with one made by Davy : 

" I thank God I was not made a dextrous manipulator; the 
most important of my discoveries have been suggested to me 
by my failures." 

Most mathematicians are the speculative type. The following 
remarks are attributed to Newton, Whewell and Gauss respec- 
tively : 

" No great discovery is ever made without a bold guess," 

" Advances in knowledge are not commonly made without 
some boldness and licence in guessing," 

" I have the result but I do not yet know how to get it." 

Most of the outstanding discoverers in biology have also been of 
the speculative type. Huxley wrote : 

" It is a popular delusion that the scientific enquirer is under 
an obligation not to go beyond generalisation of observed facts 
. . . but anyone who is practically acquainted with scientific work 
is aware that those who refuse to go beyond the facts, rarely 
get as far." 

The following two comments, made on different occasions, reveal 
Pasteur's views on this point : 

" If someone tells me that in making these conclusions I have 



gone beyond the facts, I reply : ' it is true that I have freely put 
myself among ideas which cannot be rigorously proved. That is 
my way of looking at things.' " 

" Only theory can bring forth and develop the spirit of inven- 

W. Ostwald classifies scientists slightly differently.'*^ He distin- 
guishes the classicist whose main characteristic is to bring to 
perfection every discovery and is systematic, and the romanticist 
who has a multitude of ideas but has a certain amount of super- 
ficiality in dealing with them and seldom works them out com- 
pletely. Ostwald says the classicist is a bad teacher and cannot 
do anything in front of others, while the romanticist gives away 
his ideas freely and has an enormous influence on his students. 
He may produce some outstanding students but sometimes spoils 
their originality. On the other hand, as Hadamard points out, 
highly intuitive minds may be very obscure. Kenneth Mees 
considers that practical scientific discovery and technology 
embrace three different methods of working : {a) theoretical 
synthesis, (b) observation and experiment, (c) invention. It 
is rare, he says, for one man to excel in more than one 
of these activities, for each requires a different type of mind.^^ 

The systematic type of scientist is probably more suited to 
developmental research and the speculative type to exploratory 
research; the former to team work and the latter either to 
individual work or as leader in a team. Dr. E. L. Taylor describes 
the organisation of a large commercial research organisation 
which employed men of the speculative type to play about with 
their ideas, but as soon as they hit on something that promised 
to be of value it was taken out of their hands entirely and given 
to a systematic worker to test and develop fully. ^° 

The speculative and systematic types, however, represent 
extremes and probably most scientists combine some of the 
characteristics of both. The student may find that he has natural 
tendencies toward one type or the other. Bancroft considers that 
often one type cannot be converted to the other. It is probably 
best for each to follow his natural tendencies and one wonders 
if many scientists have not been unduly influenced by the teacher 
under whose influence they happened to fall. The important 
thing is for us not to expect everyone to think the same way as 



we do ourselves. It is a great pity for a young scientist who is 
naturally the speculative type to come under the influence of a 
systematic type and be misguided into believing that his imagina- 
tion should be suppressed to the extent that it is crushed. The 
man who gets ideas of his own and wants to try them out is 
more likely to be attracted by research, to contribute more to it, 
and to get more from it than the man lacking in imagination and 
curiosity. The latter can do useful work on research but probably 
does not get much enjoyment out of it. Both types are necessary 
for the advancement of science for they tend to be comple- 

As is mentioned elsewhere, it is a common error among 
philosophers and writers of books on the scientific method to 
believe that discoveries are made by the systematic accumulation 
of data until the generalisation is a matter of plain logic, whereas 
in fact this is true in probably a minority of cases. 

The scientific life 

Some comment on the personal aspects of research might be 
helpful to the young man or woman contemplating taking up a 
scientific career. 

The young scientist on reading this book might be alarmed at 
the demands made on him and, unless he is one of those rare 
individuals who is willing to give his whole life to "a cause", he 
may be put off research if some further comment is not offered. 
Let me reassure him at once that this is a counsel of perfection 
and one can become a good research worker without sacrificing 
all other interests in life. If one is willing to regard research as 
a calling and to become what Einstein calls a tiTie devotee, all to 
the good, but there are plenty of examples of great and successful 
scientists who have not only lived normal family lives but have 
managed also to find time for many outside interests. Until recent 
times research was carried on only by the devotees, because the 
material rewards were so poor, but nowadays research has 
become a regular profession. However, it cannot be conducted 
successfully on a strict 9 a.m. to 5 p.m. basis and some evening 
study is a practical necessity. One needs to have a real interest in 
science and it must be part of one's life and looked upon as a 
pleasure and a hobby. 



Research work progresses in an irregular manner and only 
occasionally is the scientist hotly pursuing a new discovery. It is 
then he needs to pour all his energies into the work and think of 
it day and night. If he has the true scientific spirit he will want 
to do this and it is crippling if circumstances prevent it. The 
research man's family usually understand that if he is to be a 
creative scientist, there are times when it is most important for 
him to be spared other responsibilities and worries as much as 
possible; and likewise his colleagues at the laboratory usually try 
and help with any other commitments he may have in the way 
of routine work or administration. This help is not Hkely to be a 
burden on his associates or family because these spurts are all too 
rare with most people. Perhaps two to six intervals each of a 
week or two every year might be average, but they will vary 
enormously from one individual to another. However, these 
remarks should not be misconstrued as an encouragement to 
develop an "artistic temperament" and lack of responsibility in 
everyday affairs ! 

When Simon Flexner was planning the Rockefeller Institute he 
was asked "are you going to allow your men to make fools of 
themselves at your Institute?" The implication was that only 
those who would risk doing so were likely to make important 
discoveries. The research man must not be put off his ideas by 
fear of being ridiculous or being said to have "a bee in his 
bonnet". It sometimes requires courage to put forward and follow 
up a novel idea. It will be remembered that Jenner confided his 
proposals about vaccination to a friend under a bond of secrecy 
for fear of ridicule. 

When I asked Sir Alexander Fleming about his views on 
research his reply was that he was not doing research when he 
discovered penicillin, he was just playing. This attitude is typical 
of many bacteriologists who refer to their research as "playing 
about" with this or that organism. Sir Alexander believes that 
it is the people who play about who make the initial discoveries 
and the more systematic scientists who develop them. This 
expression, "playing about", is significant for it clearly means 
that the scientist is doing something for his own enjoyment, to 
satisfy his own curiosity. However, with the incompetent person 
"playing about" may amount to nothing more than ineffectual 



pottering in which nothing is followed up. Sir Henry Dale, 
speaking at a Congress held in Cambridge in 1948 in honour 
of Sir Joseph Barcroft, said that the great physiologist always 
regarded research as an amusing adventure. Speaking at the 
same Congress, Professor F. J. W. Roughton said that for 
Barcroft and for Starling, physiology was the greatest sport in 
the world. 

The great pioneers of science, although they have defended 
their ideas feH^ently and often fought for them, were mostly at 
heart humble men, for they realised only too clearly how puny 
were their achievements compared to the vastness of the as yet 
unknown. Near the end of his life Pasteur said : " I have wasted 
my life" as he thought of the things he might have done to 
greater profit. Shortly before his death Newton is reported to 
have said : 

" I know not what I may appear to the world, but to myself I 
appear to have been only like a boy playing on the sea-shore, and 
diverting myself in now and then finding a smoother pebble or a 
prettier shell than ordinary, whilst the great ocean of truth lay 
all undiscovered before me." 

Diversion and holidays are very much a question of individual 
requirements but freshness and originality may be lost if the 
scientist works unremittingly for too long. In this connection a 
good maxim has been coined by Jowett : "Don't spare; don't 
drudge." Most of us require recreation and variety in interests 
to avoid becoming dull, stodgy and mentally constipated. Simon 
Flexner's attitude to holidays was the same as Pierpont Morgan's 
— who once remarked that he could do a full year's work in nine 
months but not in twelve months. Most scientists, however, do not 
require as much as three months' annual vacation. 

Mention has already been made of the disappointments so 
often met in research and the need for understanding and encour- 
agement from colleagues and friends. It is recognised that these 
continual frustrations sometimes produce a form of neurosis 
which Professor H. A. Harris calls "lab. neurosis", or they may 
kill a man's interest in research. Interest and enthusiasm must 
be kept alive and this may be difficult if the worker is obliged 
to plod along on a line of work which is not getting anywhere. 



In most walks of life it is possible to get into a groove, or to go 
"stale", but it is a more serious problem in research than in most 
other occupations, because practically all the research worker's 
activities must be initiated from within his own brain. He gets 
stimulus from his work only when he is making progress, whereas 
the business man, the lawyer and the physician are constantly 
receiving stimulus both from their clients and from the fact that 
they are able to effect something. 

Frequent discussion of one's work with associates who show 
an interest in it is helpful in avoiding "lab. neurosis". The great 
value of "mental catharsis" in neurosis is well known, and 
similarly telling others of one's problems and sharing one's dis- 
appointments can help the baffled research worker from suffering 
unduly from worry. 

"Lab. neurosis" is most likely to arise in scientists devoting all 
their time to one research problem. Some individuals find 
sufficient relief if they have two problems under investigation at 
the same time. For others it is better to spend a portion of their 
time in teaching, routine diagnostic work, administration or 
similar occupation which enables them to feel they are doing 
something effectively and contributing something to the com- 
munity even if getting nowhere with the research. Each case needs 
to be considered individually, but if effective research is to be 
accomplished the scientist nevertheless has to devote the major 
portion of his time to it. 

With regard to this latter point W. B. Cannon waxes eloquent : 

" This time element is essential. The investigator may be made 
to dwell in a garret, he may be forced to live on crusts and wear 
dilapidated clothes, he may be deprived of social recognition, 
but if he has time, he can steadfastly devote himself to research. 
Take away his free time and he is utterly destroyed as a contri- 
butor to knowledge." ^^ 

It is little use to squeeze research into an hour or two of spare 
time during a day occupied in other duties, especially if the other 
duties are of a nature that require a lot of thought, for, apart 
from time at the bench, research requires peace of mind for 
reflection. Furthermore, to achieve results in research it is some- 
times necessary to drive oneself in the face of frustrations and 
it may be a disadvantage to have a too ready alternative "escape" 



activity. F. M. Burnet considers that part-time research is usually 
"of relatively unimportant character". 

Piatt and Baker suggest that a research worker may have to 
choose between having a reputation as being good natured and 
easily accessible to visitors but mediocre, or on the other hand 
temperamental but successful. Visitors to laboratories who are 
merely scientific sightseers ought to be severely discouraged, but 
most research workers are glad to make time to talk to visitors 
who have a genuine and serious interest in their work. 

Just before his death Pavlov wrote : 

" What can I wish to the youth of my country who devote 
themselves to science? Firstly, gradualness. About this most 
important condition of fruitful scientific work I can never speak 
without emotion. Gradualness, gradualness, gradualness . . . 
never begin the subsequent without mastering the preceding . . . 
But do not become the archivist of facts. Try to penetrate the 
secret of their occurrence, persistently searching for the laws 
which govern them. Secondly, modesty ... do not allow haughti- 
ness to take you in possession. Due to that you will be obstinate 
where it is necessary to agree, you will refuse useful and friendly 
help, you will lose your objectiveness. Thirdly, passion. Remem- 
ber that science demands from a man all his life. If you had two 
lives that would not be enough for you. Be passionate in your 
work and your searching." 


Enthusiasm is one of the great motivating forces, but, like any- 
thing associated with emotion, it can be fickle. Some people are 
given to bursts of intense enthusiasm which are short-lived, 
whereas others are able to sustain their interest for long periods, 
usually at a more moderate intensity. It is as well to learn as much 
as possible about oneself in this, as in other respects. Personally, 
when I feel myself in the grip of an enthusiasm, warned by past 
experience, I try to assess the situation objectively and decide 
if there is a solid foundation for the enthusiasm or if it is hkely 
to burn itself out leaving that deflated feeling from which it is 
difficult to rouse further interest in the subject. One help in 
sustaining interest in a subject is to share that interest with 
colleagues. This also helps to sober one up and check ill-founded 
bursts of enthusiasm. Young people are especially liable to get 
excited about their ideas and be impatient to try them out without 



giving them sufficient critical thought. Enthusiasm is a most 
valuable stimulant but, like most stimulants, its use needs to be 
tempered with a proper understanding of all its effects. 

If the young scientist succeeds within a year or two of 
graduation in establishing a profitable Une of work, it is as well 
for him to pursue it to the exclusion of other subjects, but 
generally it is wise for him to gain some breadth of experience 
before devoting all his time to one field. Similarly with his place 
of work : if he is fortunate enough to find his colleagues and the 
circumstances of his position such that he is well satisfied with 
his advances, well and good, but often, especially if the scientist 
feels he is getting into a groove, a change of position is very 
helpful owing to the great stimulus that is to be had from fresh 
mental contacts and different scientific fields. I have been struck 
by this myself and others have told me that they also have 
experienced it. Perhaps every three to five years the scientist 
under forty should examine his position in this light. A change 
of subjects also is often beneficial, for working too long on the 
same problem can produce intellectual sterility. 

It is usually difficult or undesirable for senior scientists to 
change their posts; for them the sabbatical year's leave provides 
the opportunity for a change of mental climate, while another 
method is to arrange a temporary exchange of scientists between 

It is rare for a person to carry within himself enough drive 
and interest to be able to pursue research for long if he is isolated 
from people with similar interests. Most scientists stagnate when 
alone, but in a group have a symbiotic-like effect on one another, 
just as to culture some bacteria it is necessary to have a number 
of individual organisms or to start a fire several sticks are 
necessary. This is the main advantage of working in a research 
centre. The fact that there one can get advice and co-operation 
from colleagues and borrow apparatus is of secondary impor- 
tance. Scientists from the more outlying parts of the world get 
great benefit from coming to one of the great research centres 
for a period of work, and also from paying brief visits to various 
research centres. Similarly, the main value of scientific congresses 
is the opportunity they provide for scientists to meet informally 
and discuss topics of mutual interest. Great stimulus is to be 



derived from meeting people who are interested in the same things 
as ourselves, and subjects become more interesting when we see 
how interested others are in them. Indeed few of us are sufficiently 
strong-minded and independent to be enthusiastic about a subject 
which does not interest others. 

Nevertheless there are the rare individuals who have sufficient 
internal drive and enthusiasm not to stagnate when alone and 
even perhaps to benefit from the forced independence and wider 
interests that the isolated worker is obliged to take up. Most of 
the great pioneers had to work out their ideas independently and 
some — Mendel in his monastery and Darwin during the voyage 
of the Beagle — worked in scientific isolation. A present-day 
example is H. W. Bennetts who has worked in comparative 
scientific isolation in Western Austraha. He has to his credit the 
discovery of the cause of entero-toxaemia of sheep and copper 
deficiency as a cause of disease in sheep and cattle as well as other 
important pioneer contributions to knowledge. 

Lehman has collected some interesting data about man's most 
creative time of life.^^ He extracted data from sources such as 
A Series of Primers of the History of Medicine and An Intro- 
duction to the History of Medicine, and found that the maximum 
output of people bom between 1750 and 1850 was during the 
decade of life 30 to 39 years. Taking this as 100 per cent, the 
output for the decade 20—29 years was 30—40 per cent; for 40-49 
years, 75 per cent; 50-59 years, about 30 per cent. Probably 
man's inventiveness and originality begins to decrease at an early 
age, possibly even in the 20s, but this is offset by increased 
experience, knowledge and wisdom. 

Cannon says that Long and Morton began the use of ether as 
an anaesthetic when they were both 27 years of age; Banting 
was 31 when he discovered insulin; Semmelweis recognised the 
infectiousness of puerperal fever when he was 29 ; Claude Bernard 
had started his researches on the glycogenic function of the liver 
when he was 30 ; van Grafe devised the operation for cleft palate 
and founded modem plastic surgery when he was 29. When 
von Helmholtz was only 22, barely emerged as an undergraduate 
medical student, he published an important paper suggesting 
that fermentation and putrefaction were vital phenomena and 
thus paved the way for Pasteur.^* Robinson considers 28 is a 



critical age, as many great scientists have published their most 
important work at that age. On the other hand, some individuals 
continue to do first-rate research till they are past 70. Pavlov, 
Sir Frederic Gowland Hopkins and Sir Joseph Barcroft are good 

The fact that a person has not made a significant contribution 
by the time he is 40 does not necessarily mean he never will, 
for such cases have occurred, though not often. With advancing 
age most minds become less receptive to new ideas suggested by 
others and probably also arising from their work or thinking. 
William Harvey stated that no man over forty accepted the idea 
of the circulation when he first advanced it. The reason why 
many lose their productivity about middle age is often simply 
due to their having taken on administrative responsibilities that 
do not allow time for research. In other cases indolence develops 
with middle age and security, and drive is lost. Contact with 
young minds often helps to preserve freshness of outlook. What- 
ever the reasons for the frequent falling off of productivity after 
middle age, its occurrence shows that accumulation of know- 
ledge and experience is not the main factor in successful research. 

W. Ostwald considered that the frequent decrease of product- 
ivity with increasing age is due to too long familiarity with the 
same subject. The way in which accumulated information 
handicaps originality was discussed in the first chapter of this 
book. For scientists past middle age who have lost originality, 
Ostwald advocated a radical change of field of work. In his 
own case he was evidently successful in refreshing his mind by 
this means when he was over fifty years of age. 

The research scientist is fortunate in that in his work he can 
find something to give meaning and satisfaction to life. For 
those who seek peace of mind by sinking their personality in 
something bigger than themselves, science can have a special 
appeal, while the somewhat more material-minded can get 
gratification from the knowledge that his achievements in 
research have an immortality. Few callings can claim to have 
as much influence on the welfare of mankind as scientific 
research, especially in the medical and biological sciences. 
Brailsford Robertson said : " The investigator is the pathfinder 
and the pioneer of new civilisations."^* The human race has 



existed and been accumulating knowledge for only about a million 
years, and civilisation started only some 10,000 years ago. There 
is no known reason why the world should not remain habitable 
for hundreds of milHons of years to come. The mind staggers at 
the thought of what will be accomphshed in the future. We have 
scarcely begun to master the forces of nature. 

But more urgent than finding out how to control the world's 
climate, to draw on the heat stored under the crust of the earth, 
or reaching out through space to other worlds, is the need for 
man's social development to catch up with his achievements in 
the physical sciences. And whose fancy can guess at the shape 
of things to come when mankind finds the collective will and 
courage to assume the tremendous but ultimately inescapable 
responsibility of deliberately directing the further evolution of 
the human species, and the greatest tool of research, the mind 
of man, becomes itself the subject of scientific development? 


Curiosity and love of science are the most important mental 
requirements for research. Perhaps the main incentive is the 
desire to win the esteem of one's associates, and the chief 
reward is the thrill of discovery, which is widely acclaimed as 
one of the greatest pleasures life has to offer. 

Scientists may be divided broadly into two types according 
to their method of thinking. At one extreme is the speculative 
worker whose method is to try to arrive at the solution by use 
of imagination and intuition and then test his hypothesis by 
experiment or observation. The other extreme is the systematic 
worker who progresses slowly by carefully reasoned stages and 
who collects most of the data before arriving at the solution. 

Research work commonly progresses in spurts. It is during 
the " high spots " that it is almost essential for the scientist 
to devote all possible energy and time to the work. Continual 
frustrations may produce a mild form of neurosis. Precautions 
against this include working on more than one problem at a 
time or having some other part-time occupation. A change of 
mental environment usually provides a great mental stimulus, and 
sometimes a change of subject does too. 

There is real gratification to be had from the pursuit of 
science, for its ideals can give purpose to life. 




(i) It was not a physicist but a physiologist, Luigi Galvani, 
who discovered current electricity. He had dissected a frog and 
left it on a table near an electrical machine. When Galvani left 
it for a moment someone else touched the nerves of the leg with 
a scalpel and noticed this caused the leg muscles to contract. A 
third person noticed that the action was excited when there was 
a spark from the electric machine. When Galvani's attention was 
drawn to this strange phenomenon he excitedly investigated it and 
followed it up to discover current electricity. ^^^ 

(2) In 1822 the Danish physicist, Oersted, at the end of a 
lecture happened to bring a wire, joined at its two extremities 
to a voltaic cell, to a position above and parallel to a magnetic 
needle. At first he had purposely held the wire perpendicular 
to the needle but nothing happened, but when by chance he 
held the wire horizontally and parallel to the needle he was 
astonished to see the needle change position. With quick insight 
he reversed the current and found that the needle deviated in 
the opposite direction. Thus by mere chance the relationship 
between electricity and magnetism was discovered and the path 
opened for the invention by Faraday of the electric dynamo. 
It was when telling of this that Pasteur made his famous remark : 
" In the field of observation chance favours only the prepared 
mind." Modem civilisation perhaps owes more to the discovery 
of electro-magnetic induction than to any other single 
discovery. ^^ 

(3) When von Rontgen discovered X-rays he was experiment- 
ing with electrical discharges in high vacua and using barium 
platinocyanide with the object of detecting invisible rays, but 
had no thought of such rays being able to penetrate opaque 
materials. Quite by chance he noticed that barium platino- 



cyanide left on the bench near his vacuum tube became fluores- 
cent ahhough separated from the tube by black paper. He 
afterwards said : " I found by accident that the rays penetrated 
black paper."* 

(4) When W. H. Perkin was only eighteen years old he tried 
to produce quinine by the oxidation of allyl-o-toluidine by 
potassium dichromate. He failed, but thought it might be 
interesting to see what happened when a simpler base was 
treated with the same oxidiser. He chose aniline sulphate and 
thus produced the first aniline dye. But chance played an even 
bigger part than the bare facts indicate : had not his aniline 
contained as an impurity some p-toluidine the reaction could 
not have occurred.* 

(5) During the first half of the nineteenth century it was 
firmly believed that animals were unable to manufacture carbo- 
hydrates, fats or proteins, all of which had to be obtained in 
the diet preformed from plants. All organic compounds were 
believed to be synthesised in plants whereas animals were thought 
to be capable only of breaking them down. Claude Bernard 
set out to investigate the metabolism of sugar and in particular 
to find where it is broken down. He fed a dog a diet rich in 
sugar and then examined the blood leaving the liver to see if 
the sugar had been broken down in the liver. He found a 
high sugar content, and then wisely carried out a similar 
estimation with a dog fed a sugar-free meal. To his astonish- 
ment he found also a high sugar content in the control animal's 
hepatic blood. He realised that contrary to all prevailing views 
the liver probably did produce sugar from something which is 
not sugar. Thereupon he set about an exhaustive series of 
experiments which firmly established the glycogenic activity of 
the liver. This discovery was due firstly to the fact that Bernard 
was meticulous in controlling every stage of his experiments, and 
secondly, to his ability to recognise the importance of a result 
discordant with prevailing ideas on the subject and to follow 
up the clue thus given.^^ 

(6) A mixture of lime and copper sulphate was sprayed on 
posts supporting grape vines in Medoc with the object of 
frightening away pilferers. Millardet later noticed that leaves 
accidentally sprayed with the mixture were free from mildew. 



The following up of this clue led to the important discovery 
of the value of Bordeaux mixture in protecting fruit trees and 
vines from many diseases caused by fungi. ^^ 

(7) The property of formalin of removing the toxicity of 
toxins without affecting their antigenicity was discovered by 
Ramon by chance when he was adding antiseptics to filtrates 
with the object of preserving them/^ 

(8) The circumstances leading to the discovery of penicillin 
are widely known. Fleming was working with some plate cultures 
of staphylococci which he had occasion to open several times 
and, as often happens in such circumstances, they became con- 
taminated. He noticed that the colonies of staphylococci around 
one particular colony died. Many bacteriologists would not 
have thought this particularly remarkable for it has long been 
known that some bacteria interfere with the growth of others. 
Fleming, however, saw the possible significance of the observa- 
tion and followed it up to discover penicillin, although its 
development as a therapeutic agent was due to the subsequent 
work of Sir Howard Florey. The element of chance in this 
discovery is the more remarkable when one realises that that 
particular mould is not a very common one and, further, that 
subsequently a most extensive, world-wide search for other anti- 
biotics has failed to date to discover anything else as good. It 
is of interest to note that the discovery would probably 
not have been made had not Fleming been working under 
" unfavourable " conditions in an old building where there was 
a lot of dust and contaminations were likely to occur."^ 

(9) J- Ungar^^ found that the action of penicillin on 
certain bacteria was slightly enhanced by the addition to the 
medium of paraminobenzoic acid (PABA). He did not explain 
what made him try this out but it seems likely that it was 
because PABA was known to be an essential growth factor for 
bacteria. Subsequently, Greiff, Pinkerton and Moragues'*' tested 
PABA to see if it enhanced the weak inhibitory effect which 
penicillin had against typhus rickettsiae. They found that 
PABA alone had a remarkably effective chemotherapeutic action 
against the typhus organisms. " This result was quite unex- 
pected," they said. As a result of this work PABA became 
recognised as a valuable chemotherapeutic agent for the typhus 



group of fevers, against which previously nothing had been 
found effective. 

In the chapter on hypothesis I have described how 
salvarsan and sulphanilamide were discovered following an 
hypothesis that was not correct. Two other equally famous 
chemotherapeutic drugs were discovered only because they 
happened to be present as impurities in other substances which 
were being tested. Scientists closely associated with the work 
have told me the stories of these two discoveries but have asked 
me not to publish them as other members of the team may not 
wish the way in which they made the discovery to be made 
public. Sir Lionel Whitby has told to me a story of a slightly 
different nature. He was conducting an experiment on the then 
new drug, sulphapyridine, and mice inoculated with pneumo- 
cocci were being dosed throughout the day, but were not treated 
during the night. Sir Lionel had been out to a dinner party 
and before retuminsr home visited the laboratorv to see how the 
mice were getting on, and while there lightheartedly gave the 
mice a further dose of the drug. These mice resisted the 
pneumococci better than any mice had ever done before. Not 
till about a week later did Sir Lionel realise that it was the 
extra dose at midnight which had been responsible for the 
excellent results. From that time, both mice and men were 
dosed day and night when under sulphonamide treatment and 
they benefited much more than under the old routine. 

(lo) In my researches on foot-rot in sheep I made numerous 
attempts to prepare a medium in which the infective agent would 
grow. Reason led me to use sheep serum in the medium and 
the results were repeatedly negative. Finally I got a positive 
result and on looking back over my notes I saw that, in that 
batch of media, horse serum had been used in place of sheep 
serum because the supply of the latter had temporarily run out. 
With this clue it was a straightforward matter to isolate and 
demonstrate the causal agent of the disease — an organism which 
grows in the presence of horse serum but not sheep serum ! 
Chance led to a discovery where reason had pointed in the 
opposite direction. 

(ii) The discovery^ that the human influenza virus is able to 
infect ferrets was a landmark in the study of human respiratory 



diseases. When an investigation on influenza was planned, 
ferrets were included among a long list of animals it was 
intended to try and infect sooner or later. However, some time 
before it was planned to try them, it was reported that a colony 
of ferrets was suffering from an illness which seemed to be 
the same as the influenza then aflfecting the people caring for 
them. Owing to this circumstantial evidence, ferrets were 
immediately tried and found susceptible to influenza. Afterwards 
it was found that the idea which prompted the tests in ferrets 
was quite mistaken for the disease occurring in the colony of 
ferrets was not influenza but distemper ! ^ 

( 1 2) A group of English bacteriologists developed an effective 
method of sterilising air by means of a mist made from a 
solution of hexyl-resorcinol in propylene-glycol. They conducted 
a very extensive investigation trying out many mixtures. This 
one proved the best; the glycol was chosen merely as a suitable 
vehicle for the disinfectant, hexyl-resorcinol. Considerable 
interest was aroused by the work because of the possibility of 
preventing the spread of air-borne diseases by these means. 
When other investigators took up the work they found that the 
effectiveness of the mixture was due not to the hexyl-resorcinol 
but to the glycol. Subsequently, glycols proved to be some of 
the best substances for air disinfection. They were only intro- 
duced into this work as solvents for other supposedly more active 
disinfectants and were not at first suspected as having any 
appreciable disinfective action themselves." 

(13) Experiments were being conducted at Rothamsted 
Experimental Station on protecting plants from insects with 
various compounds, when it was noticed that those plants treated 
with boric acid were strikingly superior to the rest. Investigation 
by Davidson and Warington showed that the better growth had 
resulted because the plants required boron. Previously it had 
not been known that boron was of any importance in plant 
nutrition and even after this discovery, boron deficiency was for 
a time thought of as only of academic interest. Later, however, 
some diseases of considerable economic importance — " heart- 
rot " of sugar beet for example — were found to be manifesta- 
tion of boron deficiency. ^"^ 

(14) The discovery of selective weed-killers arose unexpectedly 



from studies on root nodule bacteria of clovers and plant 
growth stimulants. These beneficial bacterial nodules were found 
to exert their deforming action on the root hairs by secreting a 
certain substance. But when Nutman, Thornton and Quastel 
tested the action of this substance on various plants, they were 
surprised to find that it prevented germination and growth. 
Furthermore they found that this toxic effect was selective, being 
much greater against dicotyledon plants, which include most 
weeds, than against monocotyledon plants, which include grain 
crops and grasses. They then tried related compounds and found 
some which are of great value in agriculture to-day as selective 

(15) Scientists working on the technicalities of food preserva- 
tion tried prolonging the " life " of chilled meat by replacing 
the air by carbon dioxide which was known to have an inhibitory 
effect on the growth of micro-organisms causing spoilage. 
Carbon dioxide, at the high concentration used, was found to 
cause an unpleasing discoloration of the meat and the whole 
idea was abandoned. Some time later, workers in the same 
laboratory were investigating a method of refrigeration which 
involved the release of carbon dioxide into the chamber in 
which the food was stored, and observations were carried out 
to see whether the gas had any undesirable effect. To their 
surprise the meat not only remained free from discoloration 
but even in the relatively low concentrations of carbon dioxide 
involved it kept in good condition much longer than ordinarily. 
From this observation was developed the important modem pro- 
cess of "gas storage" of meat in which 10—12 per cent carbon 
dioxide is used. At this concentration the gas effectively prolongs 
the " life " of chilled meat without causing discoloration.^^ 

(16) I was investigating a disease of the genitalia of sheep 
known as balano-posthitis. It is a very long-lasting disease and 
was thought to be incurable except by radical surgery. Affected 
sheep were sent from the country to the laboratory for investiga- 
tion but to my surprise they all healed spontaneously within a 
few days of arrival. At first it was thought that typical cases 
had not been sent, but further investigation showed that the 
self-imposed fasting of the sheep when placed in a strange 
environment had cured the disease. Thus it was found that 



this disease, refractory to other forms of treatment, could in 
most cases be cured by the simple expedient of fasting for a 
few days. 

(17) Paul Ehrlich's discovery of the acid- fast method of stain- 
ing tubercle bacilli arose from his having left some preparations 
on a stove which was later inadvertently lighted by someone. The 
heat of the stove was just what was required to make these 
waxy-coated bacteria take the stain. Robert Koch said " We 
owe it to this circumstance alone that it has become a general 
custom to search for the bacillus in sputum." ^^^ 

(18) Dr. A. S. Parkes relates the following story of how he and 
his colleagues made the important discovery that the presence of 
glycerol enables living cells to be preserved for long periods at very 
low temperatures. 

" In the autumn of 1948 my colleagues. Dr. Audrey Smith and 
Mr. C. Polge, were attempting to repeat the results which 
Shaffner, Henderson and Card (1941) had obtained in the use of 
laevulose solutions to protect fowl spermatozoa against the effects 
of freezing and thawing. Small success attended the efforts, and 
pending inspiration a number of the solutions were put away in 
the cold-store. Some months later work was resumed with the 
same material and negative results were again obtained with all 
of the solutions except one which almost completely preserved 
motility in fowl spermatozoa frozen to -79 °C. This very curious 
result suggested that chemical changes in the laevulose, possibly 
caused or assisted by the flourishing growth of mould which had 
taken place during storage, had produced a substance with sur- 
prising powers of protecting living cells against the effects of 
freezing and thawing. Tests, however, showed that the mysteri- 
ous solution not only contained no unusual sugars, but in fact 
contained no sugar at all. Meanwhile, further biological tests had 
shown that not only was motility preserved after freezing and 
thawing but, also, to some extent, fertilizing power. At this point, 
with some trepidation, the small amount (10—15 ml.) of the 
miraculous solution remaining was handed over to our colleague 
Dr. D. Elliott for chemical analysis. He reported that the solution 
contained glycerol, water, and a fair amount of protein ! It was 
then realised that Mayer's albumen — the glycerol and albumen 
of the histologist — had been used in the course of morphological 
work on the spermatozoa at the same time as the laevulose solu- 
tions were being tested, and with them had been put away in the 
cold-store. Obviously there had been some confusion with the 
various bottles, though we never found out exactly what had 



happened. Tests with new material very soon showed that the 
albumen played no part in the protective effect, and our low 
temperature work became concentrated on the effects of glycerol 
in protecting living cells against the effects of low tempera- 

tures." ^^^ 

(19) In a personal communication Dr. A. V. Nalbandov has 
given the following intriguing story of how he discovered the 
simple method of keeping experimental chickens ahve after the 
surgical removal of the pituitary gland (hypophysectomy). 

" In 1940 I became interested in the effects of hypophysectomy 
of chickens. After I had mastered the surgical technique my 
birds continued to die and within a few weeks after the operation 
none remained alive. Neither replacement therapy nor any other 
precautions taken helped and I was about ready to agree with 
A. S. Parkes and R. T. Hill who had done similar operations in 
England, that hypophysectomized chickens simply cannot live. 
I resigned myself to doing a few short-term experiments and 
dropping the whole project when suddenly 98% of a group of 
hypophysectomized birds survived for 3 weeks and a great many 
lived for as long as 6 months. The only explanation I could find 
was that my surgical technique had improved with practice. At 
about this time, and when I was ready to start a long-term experi- 
ment, the birds again started dying and within a week both 
recently operated birds and those which had lived for several 
months, were dead. This, of course, argued against surgical pro- 
ficiency. I continued with the project since I now knew that they 
could live under some circumstances which, however, eludea me 
completely. At about this time I had a second successful period 
during which mortality was very low. But, despite careful 
analysis of records (the possibility of disease and many other 
factors were considered and eliminated) no explanation was 
apparent. You can imagine how frustrating it was to be unable 
to take advantage of something that was obviously having a pro- 
found effect on the ability of these animals to withstand the 
operation. Late one night I was driving home from a party via a 
road which passes the laboratory. Even though it was 2 a.m. lights 
were burning in the animal rooms. I thought that a careless 
student had left them on so I stopped to turn them off. A few 
nights later I noted again that lights had been left on all night. 
Upon enquiry it turned out that a substitute janitor, whose job 
it was to make sure at midnight that all the windows were closed 
and doors locked, preferred to leave on the lights in the animal 
room in order to be able to find the exit door (the light switches 
not being near the door). Further checking showed that the two 
survival periods coincided with the times when the substitute 



janitor was on the job. Controlled experiments soon showed that 
hypophysectomized chickens kept in darkness all died while 
chickens lighted for 2 one-hour periods nightly lived indefinitely. 
The explanation was that birds in the dark do not eat and develop 
hypoglycaemia from which they cannot recover, while birds 
which are lighted eat enough to prevent hypoglycaemia. Since 
that time we no longer experience any trouble in maintaining 
hypophysectomized birds for as long as we wish." 



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Accidental discoveries, 33 
Acid-fast staining, 166 
Age, creative, 156 
Agglutination, 29 
Air sterilisation, 164 
Analogy, 94 
Anaphylaxis, 28 
Aniline dye, 161 
Anthrax, 96 
Applied research, 126 
Attributes for research, 139 

Bacon, Francis, 3, 6, 57, 82, 118, 
Baker, J. R. 74 
Balano-posthitis, 165 
Bancroft, W. D., 25, 148 
Barcroft, Sir Joseph, 11, 153 
Bartlett, Sir Frederic, 60 
B.C.G. Vaccination, 17 
Bennets, H. W., 46, 157 
Bernard, Claude, x, 2, 42, 49, 76, 

96, 144, 161 
Bessemer, 2 

Biographies of scientists, 7 
Biometrics, 6, 19 
Blowfly attack, 97 
Broaching the problem, 8 
Bordeaux mixture, 162 
Boron deficiency, 164 
Burnet, Sir MacFarlane, 8, 57, 

75, 104, 155 
Butterfield, H., 106 
Byron, Lord, 2 

Cannon, W. B., 68, 71, 117, 154 

Celsus, 137 

Chamberlain, T. C, 50 

Chance, 27 

Change of post, 156 

Chemotherapy, 32, 44 

Chilled meat, 165 

Choosing the problem, 8 

Clue. 34 

Columbus, Christopher, 41 

Committees, 122 

Competing interests, 6 

Conferences, scientific, 7 

Congresses, 156 

Copper deficiency, 45 

Cramer, F., 146 

Creative age, 157 

Curiosity, 6i 




Dai^, Sir Henry, 28, 33, 79, 153 
Darwin, Charles, 25, 59, 69, 85, 92, 

97, 103, 140 
Davidson & Warington, 160 
Davy, Humphry, 59, 149 
Defining problem, 10 
Descartes, Rene, 74, 83 
Dewey, J., 53, 59 
Diabetes, 28 
Diamidine, 45 
Difficulties, 106 
Diphtheria toxin, 41 
Discussion, 63, 156 
Domagk, G., 45 
Duclaux, E., 27 
Dunn, J. Shaw, 28 
Durham, H. E., 29 

Edwards, J. T., 35 
Ehrlich, Paul, 44, 141, 166 
Einstein, Albert, 56, 60, 137, 141, 143 
Electricity, discovery, 160 
Electro-magnetic induction, i6o 
Enthusiasm, 155 
Errors, 115 
Ethics, 144 
Examinations, 140 
Experiments, 13 

definition, 13 

fool's, 89 

misleading, 23 

multiple factor, 21 

negative, 25 

pilot, 15 

planning, 19, 125 

recording, 17 

screening, 15 

sighting, 15 
Extrasensory perception, 108 
Evolution, 69 

Fallacy, 19, 22, 23, 116, 117 

False trails, 58 

Faraday, Michael, 58, 86, 112, 136, 

Farmers, 10 

Fisher, Sir Ronald, 19, 21, 49, 108 

Fleming, Sir Alexander, 35, 37, 93, 

152, 162 

Flexner, Simon, 152, 153 

Florey. Sir Howard, 37, 93, 136, 162 



Foot-rot, 163 
Fowl cholera, 27 
Freedom in science, 121 
Frustrations, 144 

Galvani, L., 160 

Gas storage, 165 

Gauss, 70, 149 

George, W. H., 57, 60, 90, 99, 100, 

Glycogen, synthesis, 161 
Gram's stain, 28 
Graphs, 23 
Gregg, Alan, 33, 103 
GriefF, D., et al., 162 

Hadamard, Jacques, 59, 68, 70 

Haemagglutination, 30 

Hamilton, Sir W., 149 

Harding, Rosamund E. M., 55, 57 

Harvey, William, 106, 107, 112, 153 

Herd instinct, 109 

Herodotus, 99 

Hirst, G. K., 30 

History of science, 7 

Holidays, 152 

Hopkins, Sir F. Gowland, 29 

Hunter, John, 23, 62 

Huxley, Thomas, 50, 59, 149 

Hypothesis, 41 

illustrations, 41 

multiple, 50 

precautions, 48 

use, 46 

Illustrations, 27 
Imagination, 53 
Impasse, 134 
Incentive, 60, 141 
Index, card, 5 
Indexing, journals, 9 
Influenza virus, 161 
Inspiration, 68 
Intuition, 54, 68 

psychology of, 73 
Isolated workers, 156 

Jackson, Hughlings, 10, 75, 92 
Jenner, Edward, 38, 144 
Jowett, 153 

Keen, B. A., 51 
Kekule, F. A., 56 
Kelvin, Lord, 144, 149 
Keogh, E. v., 31 
Kettering, Charles, 2 
Koch, R., 118, 166 
Kropotkin, Prince, 69, 143 


Lab. neurosis, 153 
Landsteiner, 37 
Languages, 5 
Lister, 59 
Loeb, Jacques, 64 
Loewi, Otto, 71 
Luck, 32 

McClelland, L. &: Hare, R., 30 

Malthus, 69 

Mees, C. E. K., 150 

Mendel. Gregor, 49, 108 

Metchnikoff, Elie, 70, 149 

Method, transfer, 129 

Milk fever, 43 

Millardet, 161 

Minds, scientific, 148 

Minkowski, 28 

Monkey trial, 113 

Mules, 97 

Mules' operation, 24 

Nalbandov, a. v., 167 

National jealousies, 147 

Natural history, 141 

Needham, 23 

Neufeld, 37 

Newton, 149 

Nicolle, Charles, 11, 148 

Noguchi, 10 

Note taking, 77 

Nutman, P. S., et al., 165 

Observation, 96 

induced, 102 

spontaneous, 102 
Observations, recording, 17, 104 
Occam, William of, 87 
Oersted, 160 
Opportunities, 34 

exploiting, 36 

lost, 34 
Opportunism, 33 
Opposition to discoveries, 111 
Ostwald, W., 5, 79, 150, 158 
Outsiders, 3 

Pairing, 20 

Paraminobenzoic acid, 162 

Pavkes. A. S.. 166 

Pasteur, Louis, 27, 33, 96, 97, 140, 

144, 149 
Pavlov. I. P., 62, 155 
Penicillin, 162 
Periodicals, scientific, i 
Perkin, W. H., i6i 
Planck, Max, 55, 60 
Planning, 19, 121 

categories, 121 

attack, 10 


Planning and organising, 121 

Piatt, W. & Baker, R. A., 68, 72, 77, 

Poincare, H., 68, 70, 85 
Precursory ideas, 36 
Preparation, 1 
Psychology of intuition, 73 
Publication, 136 
Pure research, 126 

Quinine, 130 

Ramon, 162 
Randomisation, 21 
Rationalise, 90 
Reading periodicals, 3 
Reason, 82 

safeguards, 86 
Reasoning, deductive, 84 

inductive, 84 
References, 9 

Research institutes, size, 126 
Research, borderline, 128 

developmental, 128 

exploratory, 128 

pot-boiling, 128 

types, 126 
Resistance to new ideas, 106 
Reward, 141, 158 
Richet, Charles, 28 
Ringer's solution, 29 
Robertson, T. Brailsford, 158 
Rontgen, 35, 160 
Roux, Emile, 41 
Rush. B.. 51 
Russian genetics, 113 

Salvarsan, 44 

Schiller, F. C. S., 83, 84, 110, 132 

Schmidt, J., 43 

Scientific bandit, 145 

Scientific life, 152 

Scientists, 139 

speculative, 150 

systematic, 150 
Scott, W. M., 74 
Secrecy, 147 

Semmelweis, Ignaz, 111, 116 
Skim-reading, 4 
Smith, Theobald, 16, 37, 89, 113 

Spencer, Herbert, 5 
Spurts, 152 
Staining, 166 
Steinhaeuser, 37 
Stimulus, 156 
Strategy, 121 
Study, I, 152 
Sulphanilamide, 45 
Suiphapyridine, 163 

Tactics, 131 
Taste, scientific, 78 
Taylor, E. L., 55, 150 
Team work, 123, 124 
Teleology, 62 
Text-books, 9 
Thinking, conditioned, 64 

productive, 53 

subjective, 81 
Topley, W. W. C, 122 
Transfer method, 129 
Trotter, Wilfred, 84, 90, 109, 112 
Twins, 20 

Tyndall, J., 58, 109, 134 
Typhus diagnosis, 30 

Ungar, J., 162 

Vaccination, 37 

Vesalius, 107 

von Bruecke, 62 

von Helmholtz, Hermann, 60, 157 

von Mering, 28 

Wallace, A. R., 69-70, 143 
Wallas, Graham, 68, 75 
Wassermann, 44 
Waterston, J. J., 112 
Weed-killers, 164 
Weil & Felix, 30, 37 
Whewell, 149 
Whitby, Sir Lionel, 163 
Wilson, G. S., 17 
Winslow, C. E. A., 117 
Wright, Sir Almroth, 16 
Writing scientific papers, 6, 91 

X-rays, 160 

Zinsser, Hans, 57, 93, 111 



For their kind permission to reproduce paintings and photo- 
graphs in this book, the Author wishes to thank the following : 

The National Portrait Gallery, for Michael Faraday and 
Edward Jenner. 

The Royal Society, for Sir F. Gowland Hopkins. 

The Director of the Pasteur Institute, Paris, for Louis 


Messrs. Macmillan and Co., Ltd., for Thomas Huxley (from 
Memoirs of Thomas Huxley, by M. Foster). 

Messrs. Allen and Unwin, Ltd., for Gregor Mendel (from 
Life of Mendel, by Hugo litis). 

Picture Post, for Claude Bernard. 

Harper's Magazine, for Charles Darwin. 

Martha Marquardt, for Paul Ehrlich (from her Paul Ehrlich, 
published by Heinemann). 

The editor. The Journal of Pathology, for Theobald Smith. 

Mrs. W. B. Cannon, for Walter B. Cannon. 

Messrs. J. Russell and Sons, for Sir Henry Dale and Sir 
Howard Florey. 

Topical Press, for Sir Alexander Fleming. 

Lotte Meitner-Graf, for Max Planck. 







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